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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 601
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 602
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 603
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 604
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 605
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 606
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 607
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 608
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 609
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 610
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 611
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 612
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 613
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 614
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 615
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 616
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 617
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 618
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 619
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 620
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 621
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 622
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 623
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 624
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 625
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 626
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 627
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 628
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 629
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 630
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 631
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 632
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 633
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 634
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 635
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 636
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 637
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 638
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 639
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 640
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 641
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 642
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 643
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 644
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 645
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 646
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 647
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 648
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 649
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 650
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 651
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 652
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 653
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 654
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 655
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 656
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 657
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 658
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 659
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 660
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 661
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 662
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 663
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 664
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 665
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 666
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 667
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 668
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 669
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 670
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 671
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 672
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 673
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 674
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 675
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 676
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 677
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 678
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 679
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 680
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 681
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 682
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 683
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 684
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 685
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 686
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 687
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 688
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 689
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 690
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 691
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 692
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 693
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 694
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 695
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 696
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 697
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 698
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 700
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 701
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 702
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 703
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
×
Page 704
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 705
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 706
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 707
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 708
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 709
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 710
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 713
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Page 716
Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Suggested Citation:"Part VI. Parapsychological Techniques." National Research Council. 1988. Enhancing Human Performance: Issues, Theories, and Techniques, Background Papers (Complete Set). Washington, DC: The National Academies Press. doi: 10.17226/778.
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Below is the uncorrected machine-read text of this chapter, intended to provide our own search engines and external engines with highly rich, chapter-representative searchable text of each book. Because it is UNCORRECTED material, please consider the following text as a useful but insufficient proxy for the authoritative book pages.

PART VI. Parapsychological Techniques

A COMPREHENSIVE REVIEW OF MAJOR EMPIRICAL STUDIES IN PARAPSYCHOLOGY INVOLVING RANDOM EVENT GENERATORS OR REMOTE VI EWI NG . James E. Alcock Department of Psychology Glendon College York Univers ity Commi ss i oned by: Committee on Techniques f or the Enhancement of Human Per f ormance Commiss ion on Behavioral an] Social Sciences and Educat i on Nat i one ~ Research Counc i 2102 Constitution Avenue, Washington, D. C. 20418

( Alcock ) As far back as h istory goes, most human be ings have viewed the world as possessing a transcendental aspect beyond the materialistic dimension to which our physical senses are limited. Be it manifested through gods who employ their unlimited abilities at whim or through natural magic, which supposedly allows those cognizant of its secrets to influence and control events through the use of charms and incanta- tions, this "transcendental temptation" (Kurtz, 1986) has always beckoned both individual and society alike. The r ise of modern science proved to be a particularly dif f icult challenge to transcendental thinking. Science succeeded best whenever it concentrated only on the material- istic world and put any considerations of spirituality aside. While successful as a strategy for understanding nature, this approach created difficulty for the many scientific resear- chers who were also religious because science came to be identified with materialism, in direct challenge to their religious beliefs. As_I have discussed elsewhere in some detail {Alcock, 1985), psychical research was born in the latter part of the nineteenth century out of the desire to bend the scientific method to the study of the putative non-material aspect of human existence. The formation of the Society for Psychical Research in England in 1882 marked the beginning of organized 2

( Alcock ) empirical inquiry into post-mortem survival. Likewise, the early work of Joseph Banks Rhine in the United States focused con this subject. Gradually, the quest narrowed to the search for evidence of psychic abilities (or "psi" in today's terminology), but underlying this search, even as it does fo' many people today, lay the dies ire to estabI ish a scienti f ic teas is for supposed non-mater ial and immortal aspects of our existence . What is psi? It is not a simple matter to def ine this term because, f or one thing, there is a lack of agreement even within parapsychology as to what is its teas ic nature . In general terms, psi includes processes which involve the transfer of information or physical influence between one mi nd and another or one mi nd and an object when no known physical channel is involved. Extrasensory perception (ESP ~ is said to involve the ability to receive information from someone's mind directly or to receive information about a distant object or setting, or even to receive information about future events which have not as yet occurred, all this w1'chout_ belief it of any known phys ical channe ~ . Psychok ines is (PK) refers to the putative ability of the mind to influence objects directly - to move them or alter the ir movement- again without recourse to any known physical channel. Psi is essentially def ined negatively in that its occurence is <demonstrated only through the elimination of all conceivable 3

(Alcock) physicalist explanations. Thus, i-f a physical explanation is overlooked, a particular event might be deemed to have been a demonstration of psi; upon discovering a the physical explanation, the psychic explanation would fall away. In recent years, in the attempt to be more rigourous, some parapsychologists have begun to take a "psi-as-anomaly" approaches. That is ~ rather than assuming that some process or phenomenon (e.g., "ESP") has occurred, "psi" is used as a label when results in some experiment are anomalous with current understanding of the way the universe operates. However, this approach has tts own problems, for there are many instances of empirical findings which are clearly anomalous but would not appear even to par-apsychologists ~ or perhaps especially to parapsychologists, to be instances of pS1 . Indeed, in order to capture the sense of what is meant when people talk about psi, it seems inescapable that one must include the notion that consciousness is directly interacting with other minds and with matter, and this interaction is unimpeded by the usual constraints imposed by the physical world. Psi, if it exists, seems intrinsically to violate certain traditional scientific assumptions about the nature of r eat ity, s uch as the notion that events cannot precede their cause. PSi processes appear to be unaffected by considerations of time or distance. No known physical matter 4

(Alcock) is capable of inhibiting them. Nonetheless, parapsychologists claim to have evidence that psi does indeed exist, although such claims continue to receive a cold shoulder at the doors of science. A BRIEF HISTORY OF PSI IN THE LABORATORY It was Joseph Banks Rhine who introduced parapsycholog- ists to the laboratory. Although a botanist by training, after obtaining his doctorate Rhine devoted his entire career to parapsychology. As a university student, he had been troubled by the conflict between, on the one hand, the religious beliefs with which he had been raised (he had originally planned to become a minister) and on the other, the skepticism about these beliefs engendered by his training in science. As did many other pioneers in parapsychology, the scientific study of putatively psychic phenomena provided a good compromise between his respect for science and his conviction that there is more to our existence than material- istic philosophy suggests . Around the time of his graduation from university, Rhine contacted and found favour with Will lam MacDouga ~ I , a lead i ng social psychologist who was also unable to accept strict materialism and who was interested in scientif ic invest~ga- tion of the psychic realm, a realm which, through the popular i ty of sp i r i tua ~ ism in the late nineteenth and ear ly twentieth centuries, certainly seemed to cry out for 5

(Alcock) investigation. (In fact, mainstream psychologists on both sides of the Atlantic had given serious consideration to spiritualists' claims, but had become disillusioned and had abandoned the quest because of the failure to find anything other than fraud). When MacDougall accepted the post of chairman of the psychology department at Duke University, he invited Rhine to work under his supervision in the investiga- tion of a body of transcripts of mediumistic communications, and this grew into a full-time position, with Rhine eventual- ly setting up his famous Parapsychology Laboratory. It is not surprising that, finding himself in a psychology department and under the guidance of a psycholog- ist, Rhine adopted an experimental psychological approach to the study of psi. As had psychologists done in their studies of "normal" human behaviours and abilities, Rhine came to depend almost exclusively upon statistical analysis as the arbiter of whether or not anything psychic was going on in his studies. Rhine built his quest for empirical evidence of psi on what, for _want of a better term, might be called the "wishing-guessing" paradigm. In the study of psychokinesis, for example, a subject would watch Lice being rolled by a machine and would "wish" the dice to come up in some prespecif fed way. Rhine would calculate the success rate over a (usually very large ~ number of trials, and then by 6

(Alcock3 means of statistical tests, would decide whether or not the observed success rate exceeded that expected if only "chance" were operating. In the study of precognition or telepathy or clairvoyance, the typical task involved a set of 25 cards consisting of 5 sets of 5 different symbols (the "Zener" deck). The subject's task would be to guess which of the five types of cards was the target card. The wishing/guess- ing paradigm was an attractive one in that it made it the likelihood of the event occurring by chance readily calcul- able. Because of Rhine's claims of above-chance scoring, there ensued in the 1930s and 1940s considerable Sedate between a number of psychologists who challenged the validity of Rhine's statistical analyses, and Rhine and his defenders. Although some of the attacks struck home, leading to changes in the ways that parapsychologists did things thereafter, the brunt of the assault on statistical grounds was successfully deflected. Although Rhine came to believe that he had clearly demonstrated the reality of psi through his card-guessinq and d$ce-rolling studies, most scientists refused to accept that claim due to the lack of replicability of the demonstrations produced by Rhine and by the belief that his research was flawed by his failure to institute adequate experimental controls. With regard to dice-rolling, for example, Rhine 7

(Alcock) himself found that as controls were made more rigourous, PK effects tended to disappear. Evidence from dice-rolling studies is no longer held in much esteem by most para- psychc 1 og ~ sts . There is a small number of "class ic" Rhine studies which are still sometimes adduced as evidence by parapsychologists, but which, because of lack of repl~cability, stand essential- ly as reports of miracles; some may believe that psi effects really were produced while others may well consider that the results were due to some sort of methodological artifact which may not be obvious from the written reports, and still others may even posit fraud as the explanation. While one must be wary when pointing the finger of fraud, and while it must be emphasized that there has never been any evidence to suggest that Rhine cheated in any way in his research, the possibility of fraud should never be overlooked completely. Some important parapsychological demonstrations by one of Rhine's leading contemporaries, S.G. Soal, have fallen into disrepute as evidence grows that Soal cheated. Psychokinesis research The history of psychokinesis research is especially relevant to this paper since the random event generator research which will be discussed in detail falls in that domain. Stanford (1977) described three phases of modern PK 8

(Alcock) research. The first of these, from 1934-1950, he labelled the "early quantitative-experimental period". It was dominated by the work of Joseph Banks Rhine and his colleagues, and as mentioned earlier, dice-rolling was the major experimental PK task. A subject would attempt to influence a die in motion so as to make it stop with a particular face up. However, as Stanford points out, the methodology was often less than rigourous in these early experiments; dice were often hand thrown or cup thrown and each of these methods is subject to bias. Moreover, there was the problem of bias in the die itself: due to the fact that the higher faces of the die are lighter, they are more likely to turn up more often. This problem was not corrected, as it should have been, by balancing the target faces across trials. In about 1944, the "quartile decline" (QD) effect was discovered: it was found that PK success is unequally distributed over the period of testing, and that there was a typical pattern in the success rate: if one divided the results for a session in four quarters, the success rate for the fight quarter was higher than that for the last one. In an re-analysis of 18 studies by Rhine and his colleagues up to 1943, the vast majority showed this effect. However, Stanford points out that while the decline effect and other similar effects occasioned considerable interest because they seemed impervious to methodological artifact such as that due 9

(Alcock) to die bias, he points out that die bias can cause such internal effects, and that spurious internal effects could be caused by a number of factors having nothing to do with psi. At any rate, from 1944 to 195', more research was carried out looking at internal effects, exploring new testing methods, and attempting to overcome methodological problems. Stanford refers to the period from 1951-1969 as the "middle period". Here the die face method fell into relative disuse as the "placement" method superseded it to a large degree. With this method, the subject attempts to influence an object such as a die or ~ ball to move in one direction or another during its roll. However, this methodology, as had d$e-rolling, failed to yield convincing data. As Stanford commented, "The 1960s evinced a clear decrease in the number of PK studies done and reported. Some inves- - tigators seemed to feel that PK results were difficult to get and were weaker and less reliable than in the case of ESP" (p. 3281. Contemporary PK research has, in Stanford's view, been revolutionized by the introduction of electronic random event generators (REGs). Such apparatus appeared to answer the demands of critics of Rhine's work, such as C.E.M. Hansel, who had called for the use of automated equipment which would both produce the targets at random and record and analyze the 10

(Alcock) scores. The use of such equipment would mean that one could be reasonably certain that any observed departures from chance were not due to biases in the target sequences, or to errors in recording or analyzing the data, or to "sensory leakage" (i.e., the transmission, consciously or unconscious- ly, of information about a target from a sender to a receiver by normal sensory channels). Parapsychology and Quantum mechanics The decay of radioactive materials occurs when a sub- atomic particle takes a quantum leap from one energy level to a lower one, with the decrease being manifested by the emission of a sub-atomic particle (or ray). Such decay and particle emission is considered by quantum mechanical theory to be a truly random process, in that there is in principle no way to predict when such an event will occur. Such a process, then, provides a perfect source of randomness for a random number generator, and all one has to do is to set up some cyclical electronic process, (for example, repetitively cycling_through the digits 1, 2, 3, and 4) which is stopped by the quantum emission, yielding a random number. In principle, one could use any range of numbers. Usually, in parapsychological research, the number of alternatives is limited, with a binary output (two possible numbers) or four outputs being the most common.

~ Alcock ~ Such equipment seems naturally suited to the study of ESP where it is important to generate a target series which is unique and unbiased, but how can the equivalent of a random generator be used to study the ability of the mind to directly influence matter? The answer to this is to direct PK towards the random-generator itself; if the generator output is clearly non-random while the individual Is attempting to influence it, but is random at other times, then this would seem to support the PK hypothesis. Indeed, if PK does exist, it would appear an eas let task for the human mind to influence an electronic or sub-atomic process than to deflect a die in mid-flight. However, with the die at least one sees the target and understands the task. With a random event generator driven by radioactive decay, it is difficult to imagine how one would identify which atom is about to decay next in order to postpone it for a brief interval, and it is also difficult to imagine what form the wish might take. While one might well imagine that subjects in a die-rolling study in which the goal is to produce more sixes might be repeating over and over to themselves "Come on, six, come on", what would one wish for in the quantum case? Would it be "Don't jump, don't jump"? (As we shall see, some para- psychologists have more or less determined that one need not know anything at all about what is actually going on at the quantum level; all that is necessary is that they work their 12

( Alcock ~ wish upon the ultimate mani fe~tation of that quantum process, be it the lighting of ~ particular lamp from amongst a set of lamps Or whatever. The use of a radioactive source as the basis of randomness not only provides true randomness for pet stud.les, but once one directs one's thinking to the level of quantum i s try i nod i n mechanics, it is natural, especially when one ~ physics, to think about the possible connection between alleged psychical phenomena and some of the paradoxes about reality which are served up by quantum mechanics. Quantum theory paints a new and dramatically different picture of reality, and it is to quantum theory, and especially-to some of its unresolved paradoxes' that some psi researchers have turned in recent years. An Schmidt (1979c) points out, in contrasting the world as it was understood to be in the days of an earlier champion of parapsychology' Charles Richet, (a pre-eminent physiologist and a winner of the Nobel Prize in 1913), with the world as seen by modern physics, "RIchet based his discussion of precognition on a deterministic model in which the future could, in pr inciple, be calculated from the present . Modern quantum theory, on the other hand, suggests that the future is not completely determined by the past and that there are processes, the quantum jumps, 13

( Alcock ) which are, in principle, unpredictable. Therefore, the physicist 's most basic question with regard to pr ecogn i t i on i s whe ther human sub j ects can pred i ct the outcome of quantum processes, like radioactive decay" ~ p . 2 C ~ ~ . Indeed, almost all of the work which has been care fed out in the areas under review in this paper ~ i.e., the ability to influence random number generators and the ability to describe distant sites which are being visited by a "sender", which is referred~to as "remote viewing") has been done directly, or under the supervision, of physicists or engineers. This is not to suggest that parapsychology (or "paraphys ics", as some phys icists who interest themselves in paranormal processes would have it ~ has been accepted as a legitimate area of research by these disciplines. On the contrary; only a very small of people are involved, and in many cases viewed they are viewed by the ir contemporar ies as suspicion or outright disdain. Some of them have abandoned their original discipline, while others are careful to keep the ir Interest in paranormal processes quite separate from the ir more orthodox research . The study of the mind's putative ability to influence quantum processes was pioneered large ly by Dr . He lmut Schmidt, a physicist who now dedicates himself to the study of the paranormal . Or . Robert Jahn, Dean of Engineer ing at 14

t Alc ock ) Princeton University, is also carrying out an extensive research programme in the same area, although he does not consider himself to be a parapsycholog~st or paraphysicist. As for remote viewing, the development of this area in parapsychology was carried out by two physicists, Mr. Russell Targ and Dr. Harold Puthoff, both former laser physicists. S COPE OF THE REVI EW In an area as controversial as that of parapsychology, there is often disagreement as to what evidence or which research reports really reflect the mainstream of the domain. Critics are sometimes accused of holding up poorer examples of parapsychological research as though they were representative of the best the area has to offer. In order to avoid the possibility of such charges, and in order as well to make the reviewing task more straightforward and manage- able, this present review is limited to those research papers already selected for review by a leading parapsychologist, John Palmer (1985~. His paper evaluates eight areas of parapsychology, including the two areas which this review addresses . Since he has already selected the studies which provide the best case f or remote viewing and f or menta ~ inf luence on random event generators, ~ and the present reviewer agrees with his del ineation in this regard I, there should me no apprehens i on about whether or not the stud ~ es 15

(AlCock) reviewed herein reflect the bias of a skeptical reviewer. (I have added a few more recent papers by the same authors that Palmer chose; I am sure that these would have been included in Palmer's review had they been available at the time. Their inclusion in no way changes the outcome of my evaluation). In reviewing the various research reports, the guiding principles shall be those which one would use In reviewing a submission to a psychology journal: is the experimental design adequate and is the control of possible extraneous variables stringent enough?; is the statistical analysis appropriate?; are the conclusions justliled by the procedures and data? The question of possible experimenter fraud will not be directly addressed, for it seems to this writer that there is little point in basing the accusation of fraud on the written report of someone accused of being fraudulent. If one wants to cheat, and if one has a normal portion of wit, then one would write the report in such a way as to make the cheating impossible to detect. It is only through analysis of raw data and ether extra-report aspects that one can really detect chicanery. THE WORK OF HELMUT SCHMI DT . Over the past eighteen years or so, Dr. Helmut Schmidt, a former research physicist, has promoted the use of electronic random event generators in parapsychological 16

research. As John Palmer (1985) has observed, Schmidt's psi research has passed through several rather distinct stages: In the beginning, his Investigations bore primarily on the question of whether or not psi exists. Using a modulus-4 random number generator, Schmidt would have his subjects press one of four buttons, each under a lamp, and then depending on the output of his generator, which was ultimately dependent on radioactive decay, one or another of the lamps would light up. Schmidt was able to study precognitive ability as well as PK, although. he admitted that it was not possible to totally exclude one or the other process from any given experiment. In the next phase, Schmidt moved away from the study of ESP and turned to the exclusive study of PK. Typically, he employed only two targets instead of four, and a button press initiated a short series of trials rather than a single trial. He employed various forms of feedback, including a circular display of nine lamps and a series of clicks delivered to the subject by earphones. The third Dhase becan with the publication of his , 1975), which, based are not determined ~ ~ suggests that subjects can employ PK to influence events which occurred in the past but which have not yet been observed. This theory led him to shift his Began with the quantum mechanical model of ps i ~ Schmidt on the notion that microscopic events unt i ~ they are observed . 17

research in the direction of investigation of psi effects on previously generated and recorded random series. In recent ~ears, Schmidt has shifted his focus again. While continuing to explore the ostensible effects of PK on prerecorded series of random events, instead of using an actual series of random events he now uses randomly generated seed numbers, which when fed into an algorithm will generate a final score. Again, the subject's task is to a~ter-the series in some way. After carefully reviewing the data base of Schmidt publications used by Palmer (1985) in his review, I am in agreement with Palmer that one can hardly explain away Schmidt's results in terms of chance occurrence. Almost all of the f i f teen research papers under consideration (the f ourteen reviewed by Palmer plus one additional, more recent one (Schmidt, 1985~), yielded substantial p-values. While Palmer has gone to considerable lengths to estimate an overall Z-score for the combined results from the fourteen papers (which he finds to be Z= 9.92, p<l0-12), I have no great confidence in statistics based on the conglomeration of a group of diverse studies, and I am content simply to say that Schmidt has accumulated some pretty impressive evidence that something other than chance is influencing the subjects' scores. What might this influence be? One explanation, that preferred by Schmidt and most other parapsychologists, is 18

that the influence is a psychic one, a psi ef feet brought about either by the subjects themselves, or as Palmer (1985) iscusses, perhaps by the exper imenter, Schmidt, himse ~ f . On the other hand, some critics, notably Hansel (1980), have leaned more towards an explanation based on fraudulence on the part of the experimenter. For my part, I find both of these interpretations extreme because both make assumptions that cannot be backed up simply by looking at the data or the experimental reports. To say that one has evidence of psi Just because scoring occurs at rates significantly above or below chance over a number of studies is Jumping to a conclusion, and to argue that the only way in which such extra-chance scores could have come about is through fraud is to make a s iml far leap . My own lengthy analysis of Schmidt's papers (see Appendix I ~ leads me to respect Schmidt for what ~ see as honest efforts to improve the qual ity of his research over the years. I am also impressed by his creativity; some of his experiments border on the ingenius in some respects, although the ingeniousness is often badly tarnished by unnecessary_complexity and by weak methodology. That being said, it is also my strong opinion that, with very few exceptions, Schmidt's studies are seriously flawed to the extent that there is no way of knowing whether the data are "anomalous" in some way or simply the result of the lack of empir ical r igour and good laboratory housekeeping . 19

Each of the mayor flaws, along with some general criticisms of Schmidt's research are presented below. A more detailed treatment of each of the research articles can be fould in Appendix T. General criticisms of Schmidt's work A. Disjointedness. Despite the threads which ~ i nk va r i ous studies to succeeding ones, there is a lack of systematic inquiry evident in Schmidt's work. One study does not usually follow logically from another, and Schmidt neglects to do any in-depth probing of factors other than psi which might have generated the obtained departures from chance in his experiments. Each experiment, or at least each group of two or three studies within a given research paper, tends to stand as an independent "miracle" in a sense, and having produced the miracle, Schmidt moves on without really "nailing down" just what it is that was going on. The lack of coherence in Schmidt's research thrust is perhaps most evident by the fact that he switches from one type of random event generator to another and from one type of task to another so frequently (often on an experiment to experiment basis) that it is impossible to really get to "know" his generator (see Table I). Indeed, the changes from study to study go well beyond what is suggested by Table I, since the methodology changes frequently even when the source of true randomness stays unchanged. 20

As Hyman (1981) has pointed out, were he to use one REG over and over, he would allow himself and others the opportunity to come to understand the peculiar properties of the particular generator, whatever they may be, and be in a position to debug it. As it is, we are expected to accept his word for it that there is no bias in the generator itself. B. Inadequate controls. There is a general disregard for experimental control running throughout most of Schmidt's experiments, much of which is pointed out in the detailed analyses of his studies given in Appendix I. Schmidt seems to make the unacceptable assumption that instrumentation can replace old-fashioned controls in human experimentation (Hymen, 1981~. Schmidt's research rarely involves any kind of control group. For example, it would be germane to compare a group of subjects who are both allowed play sessions and allowed to decide when to start the test runs with a group allowed play sessions, but for whom the test runs begin at prespecified times. It would also be useful to run trials on which there is no feedback for comparison with those for which there is feedback. Without feedback, the subject would have a difficult time keying in to short term biases. Schmidt may well argue that the lack of feedback weakens the likelihood of psi either because of lessened motivation, or interference with goal-directedness, or even because observation is 21

essential (this according to his 1975 theory). (The notion that the subject needs normal, sensory feedback in order to be able to motivate or guide his/her paranormal sensory or kinetic abilities seems a bit odd, however. If extrasensory processes can reach into the future or down to the subatomic level, surely, they might just as readily provide feedback about hits and misses as well). Some of Schmidt's more recent studies have involved a control series. Terry and Schmidt (1978) included a control series of targets, but this control series turned out to show evidence of bias! C. Lack of data-snooping. Schmidt consistently fails to do the sorts of post-hoc data-snooping that one would expect in the face of findings of the kind he has produced. One would think it essential to examine the actual target series used in each of his experiments, even if one is prepared to accept that any departures from randomness are caused by PK. If, for example, there is an excess of 4s in a target series using the modulus-4 generator, it would be important to try to repeat the study and produce an excess of as or 2s or Is. If only 4s ever appear in excess, this obvious bias should be evident even to those who believe in PK. The point is that by snooping around, one might find valuable clues in the target sequence that would lead the way to a source of bias. D. Experimenter isolation. Schmidt has worked in relative isolation from other experimenters, and this of course makes 22

it more difficult to evaluate what goes on in his laboratory since we generally only have his word for it. Except for the 1986 study, his raw data is generally unavailable to other researchers and critics. E. Wild and ad hoc hy~otheseslexperimental set-ups. Schmidt, in some Of his studies, sets up experimental manipulations that are so complicated and contrived that a suspicious sort of person might suspect that in some instances part of his description of the experimental manipulation came into being after the data were examined. (This is not an accusation of fraud, but merely an allusion to the possibility that, as occasionally happens in psychology experiments, the less than rigourous researcher persuades himself or herself after the fact that the subjects were really out to obtain results different from those or~qloalty targetted). For example, in Schmidt (1970b), the subjects were encouraged to think pessimistically and in terms of failure. Yet Schmidt alluded in this paper to the notion that PK is goal-oriented- even in a complicated set of circumstances, results are obtained by concentrating only on the goal. Here the goal was self- contradictory: subjects were supposed to try to influence the lamps to illuminate successively in the direction of their choice, but they were also supposed to want to fail! Why not have them concentrate on having the sequence go °Dp°site to their preferred direction? It was actually worse than that; if the subject chose to try to make the lamps light in 23

clockwise direction counter-clockwise direction, a switch was flipped to cause a +1 number to move the illumination of the lamps in counter-clockwise direction, so that failure (an excess of -Is), which is realty success (because subjects are encouraged to psi-miss), is now ~ inked with perceived success on the board, whereas when the subject chose the , failure (excess of -Is, again which is really success) is associated with perceived failure on the board. What is the goal-directea PK going to do? Another example is that of Schmidt and Pantas (1972), where subjects were instructed to try to psi-miss the number 4 outcome of a modulus-4 REG; yet, the attempt is also made to discourage them about their ability to succeed by such failure, to the extent that they end up failing to psi-miss, which is manifested by psi-hittinq by generating an excess of 4s. F. Randomness. Since almost all of Schmidt's work requires that observed scores be compared to a "chance" score, it is critical to Schmidt's interpretation of his results to be able to assume that any bias in the data came about after the original generation of such data. It is to be expected that when a subject is trying to predict which of, say, four lights is going to be "randomly" chosen to light up next, and when there is a bias in the target sequence, the subject might quickly learn to match his or her response frequencies to the target frequencies, thus 24

leading to an increased hit rate suggestive of pr e cognition. The psychological literature, of which Schmidt, a physicist, seems to be woefully unaware, contains considerable evidence that human beings, in almost precisely the sort of situation that Schmidt has so often used, can quickly learn to match the frequency of their responses to the frequency of the diverse targets. This is referred to as "probability learning" : relative frequency judgements tend to match the actual relative frequencies in such experiments (e.g., Estes, 1976; Radtke, Jacoby, & Goedel, 19711. In the PK situation as well, if there is a short term bias in the target series, we might expect that subjects will be able, at least in some cases, and depending on the degree of bias, to detect it. For example in the case of Schmidt's modulus-four generator, if one light lights up more frequently than the others, the subject might then direct more guesses toward that light, thus bringing about a higher hit rate. This criticism applies to virtually all of Schmidt's studies in which subjects actually have to do something (i.e., as opposed to the retroactive PK studies where subjects really did nothing but "wish". Indeed, using the modulus-4 generator and four lamps in the early precognition study, one subject reported that instead of using precognition, he had attempted to use PK to produce more red lamp lightings, and surely enough, subsequent analysis of the target sequence indicated an 25

excess of 4s, which gave rise to reds. Subsequently, in PK study using the same apparatus, (Schmidt & Pantas (19 7 2 ) , i n which double psl-mlsslng produced an excess of 4s), a hit occurred only when a 4 was generated. Obviously, if the apparatus was producing more 4s than it should have, on a short-term teas ts perhaps, the subject In the first study may well have detected this and believed that he was causing it, and the same bias could account for significant results in the subsequent study. Schmidt (1976) also referred to ~ pi lot study by Lee Pantas us ing presumably the same modulus-4 generator, and again the subject's task was to produce an excess of 4s, which Ache subject succeeded in doing! Schmidt (1976) also described another similar study, using the same test situation, carried out by Dr. E.F. Kelly working with the subject Bill Delmore (who has achieved some fame and/or notoriety in parapsychological circles). Again a significant excess of 4s was produced. One might think that the careful researcher might want to try the same approach with as or 2s or 1s as targets. There is certainly good reason to be ve ry suspic lous about that modulus -4 REG ! Although Schmidt's later work s hows gr ea t e r sophistication in some ways, involving two random determinations rather than one, Schmidt continues to ignore or be unaware of suggestions which would surmount some of the concerns about the generator. Hansel (1980), for example, suggested that Avers of runs be generated, and for each pair, 26

one run be designated the experimental run and the other the control run, on the basis of some random process such as a coin toss. He also urged that the experimenter be kept blind an to the nature of each run. One could extend this down to the actual level of trial within run: for each trial, one could take the next two generated targets, and assign, using another random process, one as the target and the other as a control. Then at the end, one would have both a target series, modified perhaps by the PK of the subject, and a control series against which one could more properly evaluate the effect of the subJect's attempted lnterventlon. If there were biases introduced into the generation process, these would be as likely to reflect themselves in the control series as in the target series, and thus one could rest comfortably in the knowledge that any deviations from randomness in the test series could be evaluated in light of the control series. Schmidt may of course be concerned about the possibility of the subject's PK "spreading" ("displacement effect") to influence both elements of the pair of random numbers. However, since he is persuaded that the subject does not direct his PK toward the underlying event, but rather simply concentrates on obtaining the macro- level result that he is seeking, one would think that he need not harbour any such concerns. If one examines the fifteen reports in detail, one finds that in about half of them there is no mention of 27

i randomization controls at all. In many of the other reports, Schmidt argues that the random generators have been demonstrated to be unbiased on the basis that he has run long control series which are demonstably free of bias. (See Appendix II for a detailed list of the randomization test procedure. used in the various studies). In the 11st of problems having to do with randomization checks which follows below, the numbers refer to weaknesses in this regard. which are indicated for the studies to which they apply in Table Il. 1. The test sequence is typically very much shorter than the control run. While the long control series may not demonstrate any bias, if we were to look at series of targets as short as the test series, such bias may be evident. (Short runs will have a distribution that has a greater variance than will long runs, thus producing more deviations3. 2. In the earlier studies particularly, the long control runs (randomization checks) were often run overnight or at other times when no one was about. This means that the machine was allowed to operate in a quiescent state, -undisturbed by the voltage fluctuations that might result from the plugging in of electrical instruments elsewhere on the same voltage feed, which are likely to occur much more frequently during the daytime working hours, and undisturbed as well by the presence of human beings. (Equipment which is improperly shielded may even be 28

inf luenced by the movements of a subject seated near tt . If such were the case with Schmidt's generators, subjects could learn without awareness to make movements which tend to have the consequence of increasing or decreasing their scores, as required). Also, if there were a warm-up effect, (i.e., the generator produced biased outputs until it was fully "warmed up"), then this effect would wash out over the long control runs' but could play a significant part in the short test runs. 3. Often, there is not enough information in the wr i tten repor t to i nd i cate the tempera l re let i ons h i p o f the control runs to the test runs. 4 . Whi le not re levant to the use of a binary REG, one should be careful when using REGs such as Schmidt's modulus-4 to look not only f or b las ~ n terms o f the d is tr i but i on o f the various outcomes, but also look at higher order biases , such as doublets, triplets and so on. Thus, if a 3 follows a i-4 more often than it should were there no bias, sub Sects could learn this partial contingency and use it to increase their hi ~ rates . Schmidt never checked beyond the doublet leve when using his modulus-4 generator. 5 . I n one study ~ Schmidt, 19 7 Oa I, Schmidt attempted to correct for the d i f ference In s ize between control runs and test runs by analyzing the control run data in blocks of a size similar to the test runs. He found, using a goodness of f it appraoch, that there was no bias, even us ing the shorter 29

i blocks. However, this approach fails to eliminate the problem, for all it does is to look at a frequency distribution, rather than examining the blocks themselves for independence from their neighbours. For example, the generator could produce above-average scores for the first fifteen minutes of its operation, and then settles down to slightly below average scores for another fifteen minutes. Sometimes, as in Schmidt (1970b), the outputs of the generator were reversed half way through the experiment, and it was stated that if there was a systematic bias, this would compensate. However, no data are provided for the target sequence before and after this change, and so we have no way of knowing whether there may have been a start-up effect or whatever which may have influenced the overall scores despite the change in the outputs. Such a procedure in any case only corrects for a constant bias and not a fluctuating one. G. Data pooling. In his data analyses, Schmidt typically pools the data from all the subjects. one of the three subjects in the first experiment did not score significantly higher than chance, but his data were put together with the others to yield overall significance. The problem with this approach is that if one subject, for whatever reason, were to score very highly, and this might in some instances be because of methodological artifact or even fraud, then the pooling of data might yield overall significance, whereas, it might be more reasonable to point out, for example, that one 30

subject scored remarkably well, while others did not. My objections here are perhaps picayune, but I must ask this question: Why use a number of subjects If indeed they are interchangeable? Why not do the whole study with one subject? Indeed, as will be seen later, on occasion Schmidt does exactly that. H. ~ Most of the Schmidt studies reviewed here suffer from lack of methodological rigour. He often departs from what an experimental psychologist would consider to be standard operating procedure. There is no good reason for his failure to follow sound research practices, even while in most instances this failure is unlikely to have caused any real harm. However, in some instances the problem is rather serious and indeed may well be the source of his obtained deviations from chance. (The numbers below are used in the evaluation of lack of methodological rugour in Table II). I. In a number of the studies, Schmidt serves as both experimenter and also as a subject; in at least one case, he is really the sole subject. In another (Schmidt & Pantas, 1972, second study), Pantas is the sole subject. This is a clear violation of sound research practice. 2. In many of the studies, there are varying numbers of trails and or sessions per subject. Schmidt views his studies as attempts to score above chance, and it makes no differnce in his mind if one subject contributes 3 trials and 31

i another 30. While the differing numbers of trials and sessions is not a major worry, nonetheless, it does lead to discomfort, for if one subject is particular good at detecting generator bias, and if for whatever reason that subject takes the lion's share of the trials in a given study, overall significance could result from that sole subject's scoring. 3. (a) In some of Schmidt's earlier studies, the number of trials and/or sessions was not specified in advance, and this of course allows for optional stopping. (b3 Sometimes a range was prespecified, for whatever reason, and again this allows the experimenter to stop the study within that range at a point where the results tend to confirm his hypothesis. Given the long debates in parapsychology about the optional stopping problem, one wonders why a parapsychological researcher would allow himself to build such optional stopping into his procedure, even if it can be 5 hown that it would not affect the data very much. 4. In some of the studies, the actual number of trials actually falls considerably outside the prespecified range. For example, in Schmidt (1969a, experiment I), each of the three subjects was assigned a range of trials. One finds upon examination of the data that the subject whose range was 15,000 to 20,000 trials actually completed 22,569 trials, while one of the subjects who was supposed to carry out 20,000 to 25,000 trials actually carried out only 16,250 32

trials! There is no excuse for such sloppiness, but at least it is a tribute to Schmidt's honesty in this case that he reported the sloppiness. 5. Free play. Because Schmidt's theoretical orientation leads him to try to provide conditions which will allow the subjects to feel at ease while at the same time motivating them to do well on the test runs, he very often allows the subjects to have free play time on the equipment, with feedback about their hit rate. Then, should the subject feel that he or she is in a mood to do well, the subject is allowed to begin the session. Oftentimes, as well, the subject is allowed to end the session at his or her whim. Were it the case that a random generator produced biased strings of targets over short periods of time, this would allow the subject, from time to time, to feel that he or she was "hot" because of an increased hit rate; the subject might then well ask to begin a test session. Once his or her score started to decline again, then the subject might be expected to ask to stop, when that was an option (e.g., Schmidt (19733: the subject's momentary efficiency was frequently rechecked in warmup runs before they were allowed to contrib- ute to a test session; Schmidt (1979b): subjects first made one or two unrecorded trial runs; if they still felt good about the test, they were then allowed to contribute to the test runs. When a subject returned for another session, he 33

would always begin with one or two warmup runs after which it was decided whether test runs should be undertaken or not). 6. In one experiment, some subjects chose to work as individuals, while others worked in pairs. This odd arrangement was merely reported and no reason for it was given. 7. In some cases, there was inadequate security, in that subjects were left to run test runs without the experimenter about. 8. In some cases, as Hansel (1980) has emphasized, crucial data were not recorded in non-reset/able counters. In some cases, the key information is read from counters at the end of each session, instead of being automatically summarized by machine. - Thus, there are many problems which plague most of Schmidt's research, and the greatest of these is the randomization problem. However, Palmer (1985) responded to critics' concerns about randomization tents in this way: "The critics are correct In polntlnq out that Schmidt's early randomization tests do not adequately exclude the posslbillty of short-term biases, at least those that might occur Just after the REG is activated f or a run . However, the argument is weakened by the fact that the critics have so far not been able to articulate a mechanism 34

that would produce such a bias. Short-term biases that would occur intermittently at other times would have to be consistent in direction to account for the results Schmidt found in his experiments, yet in that case they also would accumulate and thus be revealed in the randomness tests Schmidt did undertake" (pp. 104-105~. What Palmer overlooks is the fact that through free play with feedback combined with optional start/stop, the subject is in a position to exploit whatever short-term biases exist, and whatever their direction. -Thus, although in some studies, Schmidt switched the outputs of his REG from time to time as an attempt to control for generator bias through counter- balancing, this procedure does nothing to prevent such exploitation of bias. Evaluation: The Schmidt studies Helmut Schmidt is a highly imaginative researcher who deserves credit for his creative attempts to unravel the properties of PK. However, in my view, Schmidt has failed to demonstrate that PK or ESP exist, and without such a demonstration, all his other work is for naught, since one can hardly be successful in determining the properties of a phenomenon if one cannot demonstrate that the phenomenon exists. 35

My review of this data-base leads me to conclude that there is no evidence in any of these REG studies of any effect which needs explanation by reference to psi forces. None of the studies as they stand would be accepted for publication in a good psychology research journal, in my view, quite apart from their subject matter. They are all flange' some terribly so. Schmidt, having become gradually more methodologically astute, should put in every effort to lmproGe his methods even more. Most likely, in my opinion, such would lead to the elimination of any significant departures from chance expectation at all, but that remains to be seen. So long as Schmidt believes that feedback is important to the functioning of psi, and so long as he believes that optional starting and stopping is important so as to best motivate the subject and to exploit his powers when he is "hot" (in order to insure that the subject is in an appropriate mood (Schmidt, 1969b), then there will always be the danger that subjects are unknowingly exploiting short- term biases in the random target series. As long as efforts are not made to better insure that the REG output is free of bias, as could be done using the Hansel procedure, and so long as efforts are not directed at carefully analysing the actual target sequence, not Just for one subject but across subjects and across experiments using the same REG, so as to discover patterns or other biases, critics will be very 36

Al uneasy about accepting any explanation other than generator bias as the cause of the results. The Schmidt ot al (1986) study, while not perfect, provides a starting point for Schmidt and his colleagues to collect new data using procedures where the inadequacy of the REG is not an issue. THE JAHN RESEARCH A much more elegant and sophisticated research progra=~- involving Random Event Generators has been underway for a number of years at Princeton University under the aegis of the Dean of Engineering, Robert Jahn, and with the participation of two psychologists, Roger Nelson and Brenda Dunne. This present review is limited -to_-~wo unpublished research papers (Nelson, Dunne' & Jahn, 1984; Jahn' Nelson' & Dunne, 1985) which formed the balls for Palmer's (1985) review. .... _ Rather than employing a radioactive source, as Schmidt has done, as the basis for true randomness, Jahn uses the output of an electronic noise circuit. The noise output is filtered and amplified, and then it is sampled every five microseconds. Depending on whether the noise is above or below the zero level at that point leads to the generation of a positive or negative output pulse. In order to ensure that any residual bias is eliminated, the relationship of the sign of the output pulse relative to the sign of the noise is alternated on successive trials' (or ttsamplesll' in the 37

terminology of ache Jahn team - in other words, a single binary digit 3 . ~ In keeping with the more conventional usage within parapsychology, and following Palmer's (1985) example, I shall translate Jahn ' s terminology into that used by Schmidt, so that Jahn's "sample" becomes "trial", his "trial" becomes "run", and his "run" becomes "block"~. I n the f orma ~ tes ~ ser i es, general i on rates o f e i the r 10 0 or 10 0 0 per second are used, and each run compr i ses 2 0 0 tr ia Is . The count data are permanently recorded on a str i p printer as well as being entered on line into computer memory. As we ~ I, the subject rece Ives immed iate feedback via e lectronic displays which show the number of runs, the number of hits in the last run, and the average number of hits s ince some predetermined starting point . The REG and the on-l ine VAX computer independently calculate the mean of each run, and the VAX also computes the standard deviation f or every block of fifty runs. The equipment can be run in one of two modes, either manual or automatic. In the former case, the machine will generate a run only when a switch is pressed, while in the automatic mode, once started, the machine will automatically initiate a block of fifty runs. There are two types of procedure, either "volitional mode", in which case the subject chooses whether to aim for a high score ~ PK+ ~ or a low score ~ PK- ~ in a given run, or 38

"instructed mode" where some kind of random process determines which way the subject is to aim. There are also baseline runs interspersed ("in some reasonable fashion", the nature of which is unspecified} with the PK runs; in this case the subject is to exert no influence, so that these will serve as a randomization check. The choice of volitional/instructed mode and automatic/manual mode are "normally left to the preference of the operators (subjects), but they are encouraged to undertake additional series employing the other modes for comparison" (Nelson ~L al, 1984' p.10~. The formal data base consists of data form 61 series carried out on two different machines by twenty-two different subjects over a period of five years. This produced 113,890,000 trials (l.e., binary dlglts). These data were analyzed primarily by calculating simple l-tests using, of course, an empirically determined sample variance and comparing the observed mean to the theoretical mean. The major analysis is confined to the 390,200 runs which consisted of 200 trials per run. Thus' the mean of the theoretical distribution is 100. Ignoring the baseline runs, half the runs in this analysis were PK+ and the other half PK-. The mean number of hits on the PK+ runs was 100.043, significantly greater than the theoretical mean of 100 (p=.004)' while that for the PK- runs was 99.965 (p=.016). Taken together, these two types of runs yielded a mean 39

absolute deviation which was significant at the p = 3 x 10-4 level. The baseline runs (of which there were slightly fewer than of the other two kinds) produced a mean of 100.005, which did not differ significantly from the theoretical mean. Palmer (1985) has translated these figures into a more conventional "hit" rate by treating a miss in a PK- run as a hit, (since it is in line with the subJect's goal), to yield a hit rate of 50.02%, which he points out is lower than the 50.53` mean hit rate he calculated for the Schmidt studies. It is somewhat of an enigma for the researchers to find that the results for the baseline runs are "too good", that is, the resulting distribution of t-scores is "notably devoid of significantly high or low values, and has therefore a standard deviation well below the theoretical value" (Nelson et ~L, 1984, p.25~. It is conjectured that this may be the consequence of the subjects' intentions to "achieve a baseline" in the baseline condition. Nelson ~L ~L (1984) analyzed their data in terms of three variables: (13 manual versus automatic mode, (2) volitional versus instructed target choice, and (3) 100 versus 1000 targets per second. They found that the significance described above was due only to the volitional runs. (This is interesting, for it suggests that subjects tend to be ineffective when the machine chooses the goal). Results were significant regardless of generation rate, and manual versus automatic mode had no effect. 40

Jahn's team makes much of the individual differences in cumulative run score graphs, and they talk of a subject's "signature" that seems to identify a given subject for a given set of test parameters, but may vary for a given subject as the parameters are varied. However, these signatures are based on subjective interpretation and have not been subjected to statist ical analys is . The signatures on the PK+ and the PK- tasks for any given subject are rarely symmetrical and often not even similar. It is noteworthy that one subject (Operator 010) contributed 14 of the 61 series in the formal data base, and again as Palmer (1985) points out, when this subject's series are eliminated, the remaining series in the formal group are no longer significant; this subject's scoring rate is significantly higher than that of all the other subjects combined. Nelson ~L ~L (1984) also report the results of 39 exploratory series, 33 of which were contributed by only two subjects. The data from only one of the subjects was significantly different from chance expectation, while that form the other was almost at the chance level. It is of interest to note that this high-scoring subject was none other than Operator 010 again. Another set of 12 exploratory series comprising 60,000 runs were carried out using a pseudo-random event generator (a computer algorithm) rather than the REG described above. 41

This is of some theoretical interest for parapsychologlsts, for if the results of the formal series were brought about by the subjects' psychokinetic influence of the output of the noise generator, then no PK effect should be observed when a strictly determined computer algorithm is generating the positive and negative pulses. Only three subjects were involved in these series. While the data from two of the three subjects did not deviate significantly from chance, significant results were obtained across the seven series in which none other than Operator 010 was the subject. Evaluation: The Jahn research Jahn's team has gone to great lengths to try to ensure that their equipment is unbiased. Internal circuits are continually monitored with regard to internal temperature, input voltage, etc. Successive switching of the relationship between the sign of the noise and the sign of the output pulse on a trial-to-trial basis was done to provide a further safeguard against machine bias. Results were automatically recorded and analyzed. Extensive tests of the machine's output and its individual components were also carried out at times separate from the test sessions. The provision of baseline trials interspersed with test trials provided a randomization check which overcame some of the weaknesses of Schmidt's procedure. 42

Nonetheless, despite all this machine sophistication, ~ sti ll f ind fault with regard] to procedure . An important control condition is st! ~ ~ missing: does the machine when unaf elected by the attempted inf thence of the sub ject produce output consistent with theoretical expectation- spec i f lea ~ ly, are the baseline data in line with such expectation, for they certainly were not in the data presented by Nelson ~L al (1984~. A variation of the Hansel control recommended for the Schmidt studies might be useful here: one cou ld use a random process to decide whether the next run will count as an experimental run or a control run. Our ing control runs, the subject could be seated at the console but do ing nothing, and of course, the subject would be bI ind as Deco the nature of the control run ~ BL, PK+, PK- ~ . By accumulating scores for all three conditions, one could truly, and on a dynamic basis, evaluate the unbiasedness of the hardware. Since the subject would not know whether an experimental or control run were coming next, this would make tamper ins with the machine output very difficult. Palmer (19853 draws attention to the fact that there is no documentation regarding measures to prevent data tampering by subjects, and this is of some considerable importance since the subject was left alone in the room during the formal sessions, along with the REG and recording equipment, it would appear . I t is rather uncanny that only one sub ject (Operator 010 ~ accounts for virtually all of the ~ ignt f icance 43

in the three sets of studies; (one other subject in the formal series also produced significant results, but when Operator 010's results are removed, as mentioned earlier there is no significant departure from chance across the total of remaining series). I am not trying to suggest that thIs subject cheated; I am only pointing out that it would appear that such a possibility is not ruled out. Had the subject been monitored at all times, such a worry could have been avoided or at least reduced. It concerns me that there is no clear indication of how the number of baseline runs was decided, and how these were interspersed when the subject was in volitional mode. Fewer baseline trials were run, relative to the other two types, across the whole data base. How can we be sure that a clever subject was not able, after seeing the score for a run, to switch the designation of a high baseline run to PK+, and the designation of a low baseline run to PK-, thus generating significant results for the later two types and producing a baseline data that is "too good" by virtue of being devoid of the highs and lows (just as was observed in the data)? This would be more difficult to do, presumably, if the number of each sort of run were fixed in advance, and if baseline runs were scheduled on a regular basis so that any such data tampering would be more obvious. Palmer (19853 also draws attention to possible problems of data selection and optional stopping. As for the former, 44

he points out that it is not clear whether or not the distinction between formal and exploratory series was made in advance, and since the latter seem to be less significant, it may be that if one examined ~~l the series together, the overall result may not be significant. As for optional stopping, he points out that it seems that neither the total number of trials nor the number completed by each subject was specified in advance, although it would appear from his analysis of the data that this did not have any effect. Nonetheless, this again touches my concern raised in the preceding paragraph about the looseness of the procedure in this regard. In conclusion, despite the sophistication of the instrumentation used by the Jahn research team, there is still good reason for concern about the adequacy of the controls. A good control condition is needed to ensure that the machine truly is unbiased, but more importantly it is essential that more attention be paid to the procedure, particularly with regard to specification in advance of the numbers of trials of each sort and their temporal relationship to one another, and with regard to security of the apparatus and data. There is certainly a mystery here, but based on the weaknesses in procedure mentioned above, there seems to be no good reason at this time to conclude that the mystery is paranormal in nature. 44

REMOTE V! ELI No In 1974, in the pages of Nature, physicists Russell Targ and Harold Puthoff described the apparent ability of their star subject, Patrick Price, to describe remote geographical locations being visited by other people with whom they have no sensory communication, a process they referred to as "remote viewing" (Targ & Puthoff, 1974~. In their book Mind-reach (Targ & Puthoff, 1977), they provide details of the Price study and of similar studies carried out at the Stanford Research Institute (now known as SR] International) in California. They claim to have carried out one hundred successful experiments, and they emphasize that anyone can become a remote viewer. Such claims for generality and replicability are quite remarkable in the context of other research in parapsychology and therefore they merit careful analysis. In their "main series" of trials (Targ & Puthoff, 1977), a total of 39 remote viewing trials were carried out with eight subjects . There were f ive groups of trials, with five to nine trials each, and one or two subjects in each group. A pool of over 100 geographical target locations (all within about thirty minutes driving range of SRI3 was assembled by someone not otherwise associated with the experiment. For each trial, twelve targets were selected at random, and then 45

from this set of targets a single target, which was never used again, was randomly selected. (As Palmer (1985) points out, it ls not clear whether the remaining targets were put back into the pool after use, nor is the basis specified on which the random selection of the target was made). Next, while the subject and the "inbound experimenter", both unaware of the target location, remained at the SRI laboratory, two to four "outbound experimenters" drove to the target site and spent fifteen minutes observing it. During that precise interval, the subject tape-recorded his or her impressions of the target site, and drew a sketch of what he or she "saw". Once the trial was over, the subject was given immediate feedback by being taken to the target site. For each group, the transcripts of each subject's tape- recorded descriptions along with his or her sketches were put in random order and given to an independent judge, whose task it was to visit each of the target sites used with that group and to rank-order all the transcripts according to the degree to which they appeared to correspond to the site. The sum of the ranks assigned to the response for each target was then calculated, and using exact probability tables, the likelihood of obtaining such a sum by chance was ascertained. The outcomes were in most cases strlklng' and even astounding. Four of the five groups of trials produced results that were significant at the p <.02 level (one- tailed) or better, but more impressive were the results of 46

the two best subjects, Patrick Price and Hella Hammid. For seven of his nine targets, Price's response to the target was ranked number one, while Hammi<3 's responses were ranked number one on f ive occasions and two for the other four. The odds are less than one in 30,000 that this would occur by chance! Another series of studies, referred to as the "technology series", was undertaken to determine how much detail can be discerned by remote-viewing. Twelve trials were carried out using as targets seven different pieces of equipment housed within the SRI complex. Five different subjects participated, all but one of whom had taken part in the main series. This series was conducted in the same manner as the main series, except that targets were sampled with replacement, and only the subjects' sketches were used in the Judging. Multiple drawings for the same target by different subjects were stapled together, and the judge's task was to rank each response packet against each of the seven targets. (One must wonder why only the sketches were used and why they were lumped together3. Analysis of the data revealed a remote viewing effect significant only at the p < .05 level (one-tailed). Targ and Puthoff (1977) described another study in which a subject, Hella Hammid again, was required to describe the remote targets twenty minutes before the outbound experimenter was due to arrive there. Although this "time 47

travel" was Judged to be a "striking success", (the formal judging procedure yielded a result significant at the p < .05 level), not enough methodological detail was provided to allow careful evaluation. Critiques The mayor criticisms of these remote viewing studies can be grouped into f ~ ve categories: direct cuing of the judges, non-independence of trials, selection of data, failure to pr ovine adequa te contr ol cond i ~ i ons, and sub j ect ive validation. We shall examine each of these in turn. if) Direct cuing of the fudges: The most extensive critical investigation of the Targ-Puthoff studies was conducted by David Marks and Richard Kammann. First, they attempted their own replication with five subjects, but were unable to produce any significant results. They had found it necessary in thei r research to edit out of the t ranscr i pts e xtrane ous information which might provide cues to the judges about which target site was visited, while Targ and Puthoff (1977) had stated that all of the subjects' descriptions were given to the Judge in an unedited form. If there were cues which gave information as to the order of the transcripts in the series, and if the Judges were not given the list of target sites in a randomized order, there would be no difficulty matching up tramscripts and targets, most likely without even being aware of the importance of the cues. 48

Targ and Puthoff (1977) had stated that all o.f the subjects' descriptions were given to the judges in a random order. However, when Marks visited SRI, he learned from Dr. Arthur Hastings, who had been involved in the Judging of the transcipts, that the Judges were provided with a list of targets arranged to the sequence in which they had been used in the experimentation. Furthermore, when shown the transcripts for the Price trials which had been given to the judges, Marks found that they contained a large number of cues which gave clear indications of the position of transcript in the series. (Example: In the transcript for the third target, a reference is made to "yesterday's two targetstt). In order to evaluate the importance of such cues, Marks rank-ordered a subset of five of the nine transcripts from the Price series against the corresponding five target locations. (Only five were used because details of the other four had been published and Marks was already aware of the palrlngs). Using the extraneous cues in the transcripts, Marks was able to match perfectly each of the five transcripts with the corresponding target without even visiting the sites. Subsequently, Marks and Kammann had eight experimentally naive judges repeat thin blind matching for the whole series of nine targets, giving them the list of targets in the correct sequence and the randomly ordered unedited 49

transcripts. All Judges matched the first four transcr ipts perfectly, and for the whole set of nine, the ranking was much better than one would expect by chance ~ p < .0005 ~ . Next, the five unpublished transcripts, edited to remove extraneous cues, were given to two Judges who then visited the target sites in a random order and independently ranked the transcripts at each location. Their rankings were not significantly different from chance expectation. As for the Hammid trials, Marks was unable to examine a complete set of transcripts, but Hastings did show him six of the set of nine, and again Hastings recalled that he had received the list of target sites in the order in which the experiments were conducted. Of the six transcripts, four were dated, making their relative positions in the series obvious. Other cues in the Hammid transcripts were as informative as those in the Price series. However, Hastings stated that he himself had randomized the target list after receiving it in the attempt to eliminate bias, and this would seem to have eliminated the direct cuing problem, a point emphasized by Puthoff and Targ (1981) and Morris (19801. However, as we shall see later, Marks and Kammann found fault with these trials on other grounds. As for the other trials in the main series, Marks and Kammann were unable to gain access to the transcripts and other pertinent information which would allow a proper evaluation of them. They argue that it is only reasonable to 50

assume that the same sorts of errors were also made in those trials. Tart, Puthoff, and Targ (1980) responded to the Marks and Kamman direct cuing criticism by having Charles Tart., who was not involved in the original studies, edit the transcripts of the Price series In order to remove any possible cues, and then having the series rejudged by a new Judge, presenting both target sites and edited transcripts in a random order. Again, seven of the nine transcripts were correctly matched, and the results were significant at the p < 10 level. These authors also argued that the qualitative aspects of the descriptions, apparent direct hits in some cases, was being ignored in the focus on the statistical evaluation. - Marks (1981a) responded by criticizing the fact that the editing of the transcripts was carried out by one of the investigators in the rejudging (Tart) rather than by a neutral party, and arguing that since materials regarding four of the nine trials have been published, it is only valid to rejudge the remaining five trials. Morris (1980) viewed the rejudging of the Price series by Harks and Kammann as an inadequate test of the remote viewing hypothesis since the power of the test was considerably reduced by using only slightly more than half the data, an argument repeated by Palmer (19851. Morris (1980) made several other criticisms of Marks and Kammann's 51

critique, the bulk of which were withdrawn in his response (Morris, 1981) to Marks (1981a) rebuttal. Finally, Marks and Scott (1986) reported that after three years Puthoff has finally released the relevant data about the series with Price. When they compared the original transcripts against Tart's edited versions, they were shocked to find that Tart had failed to eliminate a number of potentially useful but extraneous cues about the subject's location on each trial- indeed, eight of the nine transcripts retained extraneous cues. Given that the list of subject locations and the list of target sites had already been published in their correct order in Mind-Reach, then these cues would permit anyone familiar with that book the opportunity to match the descriptions with the targets on that basis of those remaining cues. (2) Non-~dependence of to: Apart from the groups of trials carried out with Price and Hammid discussed above, the other groups of trials in the Main series each involved trials by more than one subject. Although Marks and Kammann (1980) were unable to examine the transcripts for these groups, they point out that Hastings stated that each subject tended to focus on certain aspects of a target site and exclude others; for example, one subject apparently tended to describe architectural and topological features while another tended to describe the actions and behaviour of the exper imenter . Furthermore , transcr ipts included the 52

subject's name on the top of the page. such features of the transcripts lead to another error in the statistical analysis. Consider the case where two subjects completed four trials each, and the set of eight was evaluated as a unit: If the Judge were aware of which subset of sites a given subject had visited, then he or she could score well above chance by ranking each subject's four transcripts against his or her four targets, cutting the odds against accurate ranking in half, which would make the rank analysis used by Targ and Puthoff totally inappropriate. Hyman (1977), in one of the very first critiques of remote viewing research, pointed to another problem: the statistical analysis employed by Targ and Puthoff assumes that the trials are independent of one another. Yet, he argued, such independence is vitiated by the fact that immediately after giving his or her description, the subject was taken to the target site in order to obtain feedback about how successful he or she had been. Unfortunately, this has the effect of making the next description no longer independent of the first target site: Since target sampling in the main series was without replacement, the subject might naturally tend to avoid giving responses corresponding to targets already used, so that, for example, if the first two targets were a municipal swimming pool and a marina, then on the third trial the subject would be likely to avoid features of swimming pools and mar inas . Hyman argued that, in 53

principle, this would give a Judge sufficient information to make perfect matches at each site from the descriptions. Targ, Puthoff and May (1979) tried to defuse this criticism in saying that the target pool was large enough and the targets overlapping enough to make this problem insignificant, and Palmer (1985) points out that this criticism does not apply to the technology series where sampling was carried out with replacement. (3) Data selection: In analysing the transcripts for the Hammid series, Marks and Kammann found that drawings were missing for three of the six transcripts, and they wondered if the drawings had not been deemed accurate enough for the Judging process. They also found a number of references in the transcripts to trials which apparently had not been reported by Targ and Puthoff in their description of the research with Hammid. In the Technology series, one to five experiments are combined from each of five different subjects, but Marks and Kammann wonder by what criteria Targ and Puthoff decided to include one trial each from three subjects, four from another, and and five from Hella Hammid. They also point to indications that not all drawings were made available to the Judge in this series. Since Targ and Puthoff refer in their reports to other "demonstration-type experiments", they wonder whether other visitors ever tried the task, and if they did, were their efforts only counted as demonstrations 54

and not experiments? They conclude that It is likely that when visitors came to try remote viewing, and the results were good' these were Experiments but if the results were not so good, they were labelled "demonstrations", and excluded from analysis. : The various problems described above were in a sense made possible because there were no control tr ials to provide a base rate of transcr ipt- target correspondence when no remote viewing had occurred. This rate may be considerably higher than the theoretical chance level due to var ious methodological artifacts, such as those discussed above. Calkins (1980) offered an example of how such studies should have been run: The subject should submit not only a sketch corresponding to his/her "perceptions" during the agent's visit to the site, but also a control sketch generated under the guise of another remote viewing ef fort when in fact, unknown to the subject, there was no target site and no outbound experimenter. Then the judges should be required to match both taken from rank ing of number o f picture of happening. sketches against a photograph of the target site the agent's vantage point. By comparing the the "experimental" and control sketches across a target sites, one would have a much clearer whether or not anything extraordinary were 55

Not only was there no control condition, there are indications of considerable carelessness and sloppiness in the running of the study and the reporting of the data. For example, Marks and Kammann (1980) draw attention to the fact that the published photographs which Targ and Puthoff have used to bolster the impact of their remote viewing results were taken after the fact; it is easy to add to the illusion of a good match by choosing to photograph the site from a vantage point that highlights those features mentioned in the transcript. Again, Hyman (1977) expressed concern that since the subject and the team of investigators all went to the target site and openly discussed how good the description was, there is the danger that gossip might have trickled back to potential judges. He adds that similar concerns could be raised about the security of the protocols and the recording of judges' ratings. {5) Subjective validation: Statistical analyses aside, it seems clear from the reports that subjects and judges alike were often struck by the correspondences between the subjects' descriptions and the target sites. Marks and Kamman (1980) studied the reactions of their own subjects and judges, and found that a subject and a judge might both fee] very strongly about a correspondence between a transcript and a target, even when the judge was clearly in error and was matching the transcript to the wrong target. They concluded that when a subject or a judge visits a site at the end of a 56

trial, he or she tends to notice the matching elements and ignore those that do not match, leading to an illusory validation of the remote viewing effect. Kammann was told by Puthoff that remote viewing results do not always reflect what the outbound experimenter actually observes on the site, but that the observer acts as a beacon relaying information, even from parts of the target site which are not visible or not actually observed directly. This, Marks and Kammann (1980) argue, makes it all too probable that one can find a correspondence between virtually any report any of these complex targets, and once the correspondence is focused on, the process of subjective validation will work to persuade everyone, experimenters, subjects and judges, that there was a direct hit. Moreover, if information which does not fit is not taken into account in the evaluation, then the more a subject says, the more likely it is that a hit will be subjectively perceived (Karnes and Susman, 1979~. Summary: Given these various criticisms, there should remain little doubt that the Targ-Puthoff studies are fatally flawed, and that rather than trying to save something from them by arguing whether or not a given flaw pertains to a given subset of trials, remote viewing proponents should instead design and run a proper, well-controlled experiment with an appropriate control group. - 57

Attempts to repl icate remote viewing As already discussed, Marks and Kammann were unable to replicate the remote viewing effect despite serious effort to do so. However, there have been a number of other replication attempts, some successful, some not. Most of these have attempted to improve upon the Targ-Puthoff procedures by eliminating one or another source of artifact. (a) The Dunne studies John Bisaha and Brenda Dunne have carried out a number of remote viewing experiments. They carried out a replication of the Hammid precognitive remote viewing study, with Dunne as the agent, and obtained positive results (p<.OOB, one- tailed); four of the eight trials resulted in direct hits (Dunne and Bisaha, 1979). While they had improved on the Targ-Puthoff procedure by having eight different judges rank one description each against the eight targets, they unfortunately employed unedited transcripts, which makes one uneasy about accepting their findings. (Moreover, the percipients in this study were explicitly advised to try not to define or identify what they saw with specificity, but to stick to general impressions. This contributes to the subjective validation problem discussed earlier). As Palmer (1985) pointed out, however, the use of photographs instead of having the judges visit the sites introduced another bias, in that both the photographs and the transcripts may 58

photographs may bear regard to indications resorted that the v correspondence to one another with of weather conditions. (The authors _ had f ound no such cues in the photographs ~ . It would also appear that Hyman's (-1977) concern about sub jects, following feedback, avoiding descrip~cions which might apply to the previous targets, wasnot ruled out. Bisaha and Dunne ( 1979 ~ conducted precognitive remote viewing studies. signif icant results in line with the two additional Each produced remote vi ewi ng hypothes is . The more interest ins of these involved trans- Atiantic remote viewing. Each morning over a period of f ive consecutive days, ache percipient, in the United States, attempted to descr the where the agent, in Eastern Europe, would be 24.S hours later. The agent was then to spend 15 minutes at the appointed time the next day attempting to concentrate on the surround ings and tak ing a photograph which would later be compared against the percipient's description. Upon his return the agent gave the five photographs and brief descriptions of the target sites, in random order, to the percipient to rank order ~ ~ way. The percipient also gave to :~ ~ ~ transcripts, in random order, for the experimenter to rank against the targets. Finally, a third person, who had no other connection with the experiment also rank-ordered the photographs against the descriptions. All three rankings 59 n the usual the exDer imenter a set of

were significant (p< .025, .025, .05, respectively, all one- tailed). Dunne, Jahn and Nelson (1983) set about to develop an analytical scoring technique for remote viewing studies. Both sender and percipient were required to code their perceptions of the target in terms of 30 binary descriptors (such as indoors or outdoors). They then empirically derived a baseline distribution of chance scores by the analysis of 42,000 mismatched permutations of targets and perceptions. Next, they examined the data from some 300 separate remote vi ewi ng tr ia is, most of wh i ch were of a precogn it ive nature, which ranged over phys ical separations of up to ll, 000 mi les and time intervals of more than 48 hours. They applied several different scoring methods to assess the correspondence between two sets of 30 binary bits and found that the composite z-scores calculated for the total sample were highly significant regardless of method of scoring. As Palmer (1985) has already pointed out, since no procedural details about most of the trials are included in the report, one cannot offer a methodological critique. (b) The Schlitz studies Schlitz and Gruber (1980) conducted a long-distance remote- viewing experiment with Schlitz, in Detroit, as percipient and Gruber, in Rome, as agent. Gruber, over a period of ten consecutive days and at preset times, visited various targets in Rome which had been selected randomly from a target pool, 60

without replacement. At the times that Gruber was at the target sites, Schlitz recorded her impressions. Following the completion of all ten trials, Schlitz sent a copy of her ten protocols to Gruber, still in Rome, and he and another individual who was blind to the target translated the protocols into Italian. They also checked for cues in the transcripts that might allow judges to infer temporal order, but none were found. The percipient's sketches were photocopied and attached to copies of the protocols. Each of five Judges rank-ordered the protocols against the target sites. Highly significant results were obtained for the combined rankings of the five judges, and also separately for four of them. To eliminate the possiblity that the agent and percipient, being people of shared interests, may both be tuned to events going on in the world about them which will lead them, at any given time, to focus more on certain characterisitcs (such as the weather), thus leading to an artifactual correspondence between their reports, the authors carried out a rejudging of these data (Schlitz and Gruber, 19817. Two new Judges in Rome were asked to rank the percipients's impressions against the target sites, but were not given the agent's impressions. The scoring was carried out as before, and the results were found still to be significant but at a reduced level. 61

As Palmer (1985) observed, it is note stated in the report whether the transcripts were given to Gruber in random order or whether the Judges received the target list in random order. It is also unacceptable that the translation and ed iting of the transcripts involved Gruber, who knew the order of the target sites. For all these reasons, this study would not have been accepted for publication in a good psychology journal' its parapsychological nature aside. In a subsequent study (Schlitz & Haight, 1984), these problems were eliminated. Schlitz, in North Carolina, served as percipient while her co-experimenter served as agent in Florida. Ten target sites were randomly chosen without replacement from a pool (number unstated) of target sites, and the agent visited a different target.site for 15 minutes on each of ten days; at these same times, the percipient recorded her impressions of the agent's location. Agent and recipient sent their materials (typed transcript of tape- recorded impressions from the percipient, and final target order for the agent) to a third party' who randomized both the transcripts and the list of locations, and sent them, along with rating sheets, to two Judges. There were no notes from the agent; there was no direct communication between agent an percipient until after the experiment.was over, and the percipient received no feedback until well after the experiment was over. Subsequently two Judges went together to each target site and evaluated the correspondence between 62

the site and the percipient's description. The results were significant at the .05 level one-tailed. This study is the best controlled of all the remote-viewing reports examined so far, a point upon which I am in agreement with Palmer (19861. {~) The Karnes studies Karnes and Susman (1979) conducted a remote viewing experiment within the framework of a signal detection experiment. Signal detection theory provides a powerful method for detecting a signal, if one is present. Unlike the other studies mentioned so far in this survey, this study was set up with a control condition. Moreover, rather than depending on the vagueness of the percipient's reports and the arbitrariness of the judging, this study presented each percipient with a response booklet in which 18 sites were represented' each on a separate page' by four photographs of the target site taken from different vantage points. While the agent was on the site, the percipient was to select one or more of the I~ sites as possible locations for the sender, and to rate the confidence of each selection on a five point rating scale. Of the 18 sites, only 9 were actually used, and the others where "noise" sites. In addition, there were two other sites which were not represented in the set of 18, and these were used to provide a sort of control condition. There were a total of 10 receivers for each of the 9 targets and 25 receivers for the 63

two control group targets. The results did not statistically differ from chance expectation. Karnes, Ballou, Susman and Swaroff (1979) conducted another remote viewing experiment with a different sort of control, this one a full fledged "control group". Each subject participated in two remote viewing trials, but half of the subjects did not have any contact with the sender before the first attempt, whereas the other half of the subjects met the sender immediately prior to the commencement of the trial. The authors reasoned that if the receiver is unaware of both the identity-and location of the sender, then the receiver's impressions should be self-induced, and would serve as a control for guessing (response bias). After the first trial, the receiver and sender met at the target site and there was no llmltatlon placed In their dlecusslon. The second trial was identical for both groups of subjects and similar to the traditional remote viewing trial. Judging was carried out using both a confidence rating scale and a rank order scale. A set of 120 judges evaluated the results for trial 1 and another 120 evaluated the results for trial 2. No statistical support for remote viewing was found. In trial 1, there was no significant difference in the scoring rate of the experimental and control groups. In another study (Karnes , Susman, Klusman, ~ Turcotte, 1980), the subjects were eight individuals who 64

claimed to be psychics. Again, no evidence of remote viewing was found. Evaluation of the remote viewing studies - My own view is that Marks and his colleagues have so clearly pointed out the deficiencies in the Targ-Puthoff studies that there is no sense in trying to analyse them further. Added to the clear problem of sensory cuing and the conjecture about data selection is the fact that Targ and Puthoff have been very reluctant to provide access to their raw data, and have only Just this year released a portion of it after considerable pressure was brought to bear. The result was to show that the editing that Tart had supposedly done very carefully was actually done sloppily and did not solve the problem it was intended to solve. Of the Schlitz studies, the Schlitz and Haight (1984) study was better controlled than the earlier studies or the Targ Puthoff studies; it is interesting to note that the results in this case are much less striking than when conditions were less controlled. However, one can have no confidence at all that the significant results reported in this study have any real meaning, for there was no control condition to indicate the background "coincidental" rate. The same applies to the Dunne studies, quite apart from the flaws previosly noted. 65

Karnes and his colleagues used control conditions and found no evidence of remote viewing. This does not by itself mean that the phenomenon does not exist, for one cannot prove non-existence. However, their work clearly points to the proper methodology to be used in the study of remote viewing. One must use a control condition for establishment of a baseline "guess" rate. Without such a condition, the statistically significant results of the other studies are not interpretable, for they are based on an assumed guess rate which, because of various sources of artifact airady discussed, and perhaps others not yet discovered, may well underestimate the actual guess rate. The lack of proper control conditions would keep the Targ-Puthoff, the Dunne, and the Schlitz studies from publication in a good Psychology journal, the parapsychological is demonstrated, and replicated, in well designed studies (employing control groups) executed under well-controlled conditions, there is no reason at all to take remote viewing seriously. OVERALL CONCLUS I ONS This examination fo REG and remote viewing studies leads me to the inescapable conclusion that none of this research has served to demonstrate the reality of psi phenomena. Instead, there are serious flaws and shortcomings which a good psychology theme quite aside. Until remote viewing 66

require elimination before one can have any confidence in the statistical departures from expectation. ~ f one had to s ingle out the most ser ious and recurrent problem, it would be, in my view, fiche absence of proper control groups or control tr tale . The use of the Hansel procedure in the Schmidt studies would generate control group data which would allow a direct comparison of the "experimental" data with the baseline, coincidental, "background " rate of scar i ng as empi r i cal ly determined in the control trials . I have suggested that a modif ication of this procedure could be used in the Jahn paradigm. More traditional control tr ials have also been suggested for the remote viewing research. Psycho ~ og i ca ~ r e s ear ch i s bu i It ar ound ~ he conce pt o f comparison of experimental and control conditions. There is every reason to demand a s imi lar approach in parapsychology. The arguments that ps i f orces cannot be turned of f and may equally affect experimental and control trials leading to no di f ference between the two is not acceptable . In the absence of conclus ive, or even persuasive, evidence that psi exists, there is no reason to suspend the very procedure which can serve as our strongest bulwark against erroneous interpretation of data. If the "phenomenon" disappears in such a case, then we should bother no more about it. 67

TABLE I: OVERVIEW OF STUDIES INCLUDED IN SCHMIDT REVIEW . . . ~ . . _ 1 STUDY SOURCE OF RANDOMNESS I TASK/GOAL/CIRCUbISTANCES I 1 1 1 1 1 1969a I modulus-4 quantum REG Iprecognition or PK I 1 1 i 1 1 1969b I Rand tables Iprecognition or clairvoyance I 1 1 1 1 1970a I binary quantum REG Icat, cockroaches as sub Sects I IPK 1 ~ modulus-4 quantum REG ~ internally different machine' electronic noise REG Itargets at high speeds Ivisual vs auditory f eedback [examination of role of qen- I Orator on PK per f ormance l Ipre-recorded targets Ipre-recorded targets Ipre-recorded targets l 1 1970b l l l l i 1 l l l · I l l l - ~ ~ . ~ 1972+ 1973 ~ l l 1974 1 I 1976 1978 1978* ~ l 1979a 1979b ~ l 1981 l l 1985 1986 Rand tables binary quantum REG binary quantum REG two generators, one simple, one complex electronic noise binary REG indeterminate REG- an INSAI minicomputer! binary REG IPK in cockroaches electronic die based Ipre-recorded and real-time on radioactive decaylevents, stroboscopic light ~ as reward seed numbers producedIprerecorded and preinspected by binary quantum Iseed numbers generator (modulo-1671 computer with attach-leffects of two successive ed Geiger counter IPK attempts l computer with attach-! channeling PK ed Geiger counter! ll l ll ll + with Pantas * with Terry 68

TABLE ~ I: MAJOR PROBLEMS, SCHNIDT'S CONFIR}2ATORY STU1?IES I STUDY IRA1!1DOMI ZATION CHECKS I ! ~ ' METHODOLOGI CAL I RECORD I NG I SECUR I TY I LACK OF R I GOUR ~ PRC1BLEMS I I · · ~ ~ ~ , . ~ _ ~ 11969a-11 I, 3, 4 1 2,3b,3c,4,5a,5b,91 2 1 1 I I I . I I -21 1, 3, 4 1 2, 5a, Sb, 9 1 11969b 1 Unspecified* 1 2, 5a, 5b, 6 - I I I . I I 11970a-11 1, 2 1 3a 1 I -21 1, 2 1 I 11970b 1 1, 3, 5 1 2, 7 1 . 11972+-11 Unspecified 1 4, 7, 9 1 1 1 1 1 I -21 Unspecified I 1, 9 1 11973 1 1, 2 1 1, 2 1 Il974 ~ Unspecified ~ 1, 2, 4, 5b 1 11976 -11 1 1 1 I -21 1 1 1 I I I . I 11978 -11 Unspecified I 10 1 11978 -21 Unspecified ~ 10 1 I I I 11978*-11 1 1 1 I -21 1 1 1 I -31 1 1 1 11979a 1 Unspecified I 11 1 119 79b ~ Unspecified 1 2, 5, 10 1 11981 1 Unspecified 1 2, 3c, 5 1 I I 1. 11985 1 Unspecified I 1 1 1986 ! Not needed I i, 2, 1, 2 l 1, 2 1 1 l l 2 l 1, 2** 1, 2 ~ 1, 2**1 1 2** 2** l l . I 1 l l - 1 ll l l l l l l 1 1 l l 1 1 1 l 1 1 1 1 + with Pantas * with Terry 69

(Alcock ) APPENDIX I: DETAILED CRITIQUE OF THE: SCHNI DT STUDIES Schmidt (1969a) "Precognition of a quantum process": in this report, Schmidt presented the data from two experiments which examined the abilities of subjects to predict or influence the outcome of a quantum process. Tile statistical evaluation of success In these experiments is based on the likelihood of obtaining a hit by chance if the target series is random. As is typical with Schmidt, he was the sole experimenter. The subject was seated in front of a pane] containing four coloured lamps and four corresponding push-buttons. Prior to a button being pressed, an electronic circuit was in operation such that electrical pulses, at the rate of one million per second, arrived at an electronic four position switch, and each pulse advanced the switch one step, in the sequence 1,2,3,4,1,2,3,9... Once any of the four buttons was pressed, there was a short waiting time of unpredictable length, determined by the err ival and registration of an electron from a decaying strontium-90 source. At this point, an electronic gate closed such that the switch stopped at its current position and the corresponding lamp was lit. Once the switch stopped, one mechanical counter advanced by one to indicate the number of trials, while a second such counter advanced by one only if the illuminated lamp corresponded to the button which was pressed (a "hit"). These two counters were non-reset/able, and their readings were recorded by hand. Furthermore, an external paper-tape punch recorded which lamp was illuminated and which button had been pressed. First experiment: Here, the subject's task was to try to predict which of the four lamps would next illuminate, and the aim of the experiment was to see if subjects could make such predictions at a rate signifi- cantly above what would be expected on the basis of chance alone. Schmidt points out that although the study is set up to examine precog- nition, it is impossible to rule out the possibility of psychokinesis: the successful subject could be manipulating the quantum process so as to increase the likelihood that a particular light will illuminate. There were three subjects chosen from a set of 100 potential sub- jects on the basis that they were among those who seemed to cons~s- tently score above-chance In preliminary trials. Rather than presetting the number of trials, Schmidt for some unspecified reason assigned a range of trials to each subject: one subject was to do between 15000 and 20000 trials, while each of the other two were to do between 20000 and 25000 trials. Except for some of the trials with one subject, Schmidt was present during all the trials. 70

(Alcock) Randomization checks: Five million numbers were generated by the REG for control purposes, and the frequency of all four numbers and all sixteen sequential pairs were calculated; these frequencies did not differ significantly from chance expectation. These five million numbers were recorded on 100 different days, "preferably directly after the experimental sessions". Results: The 63,066 trials from all three subjects combined yielded a hit' rate which was significantly above chance expectation (p < 2 X 10- )' although the actual hit rate was 0.261 versus the chance expect- ation of 0.250. Evaluation: There were a number of weaknesses in this study, including the following: (a) The randomization checks were inadequate. Although Schmidt tries to reassure the reader that he carefully checked to ensure that the generator operated without bias, he did not check beyond the doublet level, and he did not check for short-term biases. We are given no information about the temporal relationship between the control runs and the tests except for the "preferably after" comment. ( b ) The subject was free to "play" with the equipment ( with paper punch and non-reset/able counters disconnected) and to decide when to start and stop a given session. If there were short-term biases in the generator which lasted, suppose, for ten minutes, and which were not detected during the randomization tests (which were of much greater length), these play sessions, the feedback, and the freedom to choose when to start and stop a session provide magnificent opportunity to exploit, consciously or unconsciously (and most likely the latter) that bias. After all, the subject would want to begin a session, presumably, when it appears that he or she is "hot", while, if the subject's scoring rate declines, he or she may well want to end the session and start again later.- The subject was given immediate feedback by means of a set of resettable counters (distinct from the non-reset/able ones mentioned above ~ which displayed the number of trials and the number of hits. (c) Methodological sloppiness: It is sloppy and totally unnecessary to assign different numbers of trials for different sub j ects . I t i s equa l ly s o to prese t a range rather than an act ua l number of trials. Worse, one finds upon examination of the data that the subject whose range was 15,000 to 20,000 trials actually completed 22,569 trials, while one of the subjects who was supposed to carry out 20,000 to 25,000 trials actually carried out only 16,250 trials. This sort of sloppiness by itself would make it difficult to obtain publication in a good psychological journal. However, given the long debates in parapsychology about the optional stopping problem, one wonders why a parapsychological researcher would allow himself to build 71

( Alcock ) such optional stopping into his procedure, even if it can be shown that it would not affect the data very much. It is likely that Schmidt did so in the bet ief that Deco do otherwise would detract from allowing sub Sects to operate when at the ir best . There was again sloppiness in the distribution of sessions, which were at the subJect's whim, it appears. There were lB sessions (~l for one subject, 5 for the second and two for the third ~ and we are not told over how many days these sess i ons were spread . More over, the study was carried out, for no apparent reason, witn very few (3) subjects, despite the pretension of having selected a "team" from 100 potential subjects. (d ~ Recording: As Hansel ( 1980 ~ has pointed out, Schmidt used an automated machine, but then left the recording procedure vulnerable to recording errors since it was necessary to manually read and transcr ibe the non-reset/able counters. (e ~ Analysis of data: (i) In his data analysis, Schmidt pools the data from all the subjects. One of the three subjects in the first experiment did not score significantly higher than chance, but his data were put together with the others to yield overall significance. The problem with this approach is that if one subject, for whatever reason, were to score very highly, and this might in some instances be because of methodological artifact or even fraud, then the pooling of data might yield overall significance, whereas it might be more reasonable simply to point out that one subject scored remarkably highly, while others did not. My objections here are perhaps picayune, but I must ask this question: Why use a number of subjects if indeed they are interchangeable? Why not do the whole study with one subject? Indeed, as will be seen later, on occasion Schmidt does exactly that. ~ i i ~ No information is provided about the proportions of singlets and doublets in the actual target series, and given what is bet ng claimed, this is a serious lacuna. It would illuminate the discussion of pass ible short-term biases in the REG to know whether or not the target sequences deviated very much f ram chance expectation. Schmidt does point out that one subject in the first experiment (who reported having attempted to influence the outcome rather than just predict it) actually experienced a target sequence in which the red light (corresponding to the number 't4") come on significantly more frequently than would be expected by chance. This finding is damning evidence with regard to the inadequacy of the randomness checks, ( unless one begs the quest i on and assumes the existence of the phenomenon that Schmidt is Crying to demonstrate, in which case, as Schmidt does, one could argue that this non-randomness is due to, and evidence of, PK ~ . I f we do not assume a pr for i the real ity of ps i, then we must conclude that at least for the highest scoring subject, the sequence of 72

~ Alcock ~ targets was non-random. The subject ' s report that, on his own and without instruction, he concentrated on causing the red lamp to come on is quite consistent with the idea that he was differentially rewarded (with a hit ~ when he chose red. One would like to examine the data for the other sub jects as well, in order to explore whether or not such departures from randomness were evident in the target ser ies presented to them as we ~ ~ . One must wonder what interpretat ion Schmidt would have given to the excess of reds had the sub ject not mentioned that he had tr fed to use PK, or if the red light had lit up signif Scantly less frequently than expected; one must a Iso wonder whether or not the sub] ect made mention of PK before learning that one light had come on signif icantly more frequently? Note that the same sub ject was the highest scar ing sub ject in the f irst expel iment and care fed out all his tr ials in only two sess i ons . Second experiment: Here, subjects were allowed to choose to go after a high score (high number of hits ~ or a low score, and we are told that " [a it the beginning of each session it was decided whether to try for a high score or a low score" (p. 107 ~ . However, of the three subjects, two of whom had taken part in the f irst experiment, only one apparently ever chose to go in more than one direction. Of the remaining two subjects, one always went high and the other always went low. These latter two subjects contr ibuted 5000 trials each whi le the former contributed 10000, about 57% high and 43% low. Results: Again combining all the data, Schmidt found an overall scoring rate of 27% which is significant at the p ~ ~ 0-10 level. Evaluation: The same criticisms about randomization checks, small number of subjects, and so on which were made in the analysis of the f irst exper iment also apply here . As well, allowing the sub ject who went high on some trials and low on other trials to make that choice, presumably following the "play" period, again makes tuning in to short-term biases more likely. For example, if red seems to occur more often than it should, then one might aim high and choose red a lot; if red seems to be relatively infrequent, one might then aim low and choose red a lot. It would be very interesting to look at the raw data and as a first measure examine the distribution of subjects' choices as well as the distribution of targets. These data were not analyzed in the report. Another weakness, as Hansel (1980) has pointed out, is that recording errors were made quite possible by the fact that high and low scores were not separately recorded in the non-reset/able counters. Indeed, there was no overall deviation from chance, if one simply examined the totals shown by the non-reset/able counters, and the alleged psi effect was only apparent when the scores were broken down on the basis of whether or no the goal was high or low scoring. Hansel ~3

~ Alcock ~ was very concerned that so much manual data analys is intervened between the results shown on the non-reset/able counters, which indicated no overall deviation, and the signif icant departures from chance which were evident f allowing the manual data ass ignment and analys is . OVERALL JUD<jEMEN-: The weaknesses ~ iscussed above reduce these two studies to the status of, at best, pilot studies; the above criticisms need to be addressed before there is any reason at all to take the ps i claim seriously This report, in my judgement, were it merely dealing wi th no rma ~ ps yci~o ~ og i ca ~ phe name na, wou Id no ~ be acce pted f o r pu b ~ i c - ation by peer-reviewed psychology journals simply because of the sloppiness of the design and execution and the lack of thorough randomness checks . Wi th regard to the latter, and as ment ~ oned above, one would need both randomness checks which are of the same length as the target runs, and run during approximately the same time periods as the experimental runs. Schmidt (1969b) "Clairvoyance tests with a machine": Schmidt, again the sole experimenter in this research, views this experiment as a continuation of the '969a studies. However, rather than using a "real-time" random generator which allows for the operation of PK, Schmidt used as his target sequence a set of 100,000 digits (l,2,3,4) taken from the Rand tables and then further shuffled and again checked for randomness. These numbers were punched into paper tape. Schmidt argues that this rules out PK, allowing only precognition or clairvoyance to operate. (It is interesting to note that Schmidt obviously denies PK the power to alter the pattern of holes in a paper tape). Six subjects, two of whom had participated in the 1969a experiments, participated in this experiment. Although there Is no explanation as to why this was done, four of these subjects chose to work in two pairs, so that one subject would do a number of trials until he or she felt like stopping, and then the second subject would work at it until he or she wanted to stop and then the first would resume . This would be repeated unt i ~ they wished to end the sess i on . A subject could decide to aim for hits or misses on any given run and hen a swi tch was thrown i n order ~ o re cord on paper tape the type o f run. As Hansel has pointed out, again the high-Iow distinction was not recorded in the non-reset/able counters. There were no limits on the number of trials to be contributed by any given subject, or on the length of the sessions. It was decided in advance to run either 15000 or 30000 trials, although no reason is given as to why two figures were specified, and 15,000 were actually run. Randomization checks: The randomness check is not described in tile report, but a reference is made to an unpublished paper. 74

tAlcock3 Results: There were +108 deviations on the high trials, and -152 on the low trials, for an overall success rate of 26.7% versus the chance rate of 25~. (This is statistically significant, pa 0.6 x lo-6. . Evaluation: Again, there is a lot of sloppiness here: some subjects worked in pairs, some did not; subjects chose when to begin, end or switch, and inhere was no regulation of the number of trials per subject, and so on. However, the key question is this: if one were to examine the actual sequences of targets, were those sequences (which were short, relative to the overall set of 100,000 numbers which had passed Schmidt ' s randomness checks ~ unbiased? Us ing Schmidt ' s own words, PK is not a factor here, and so if the overall frequencies associated with singlets.. doublets and even triplets are not as one would expect from a random ser ies, then again, we might expect the sub jects to learn to exploit the biases in the ser ies . OVERALL JUDGEMENT: Given the lack of information about the randomness checks, and given that the actual target sequence was carefully analysed after the fact, the conclusions drawn by Schmidt are premature, and this paper would be unlikely to be accepted for publication in a peer-reviewed psychology journal even if only normal psychological processes were being investigated. Schmidt (1970a) ''PK experiments with animals as subjects": This report consists of two studies, one carried out with Schmidt's pet cat and the other with a number of cockroaches. In the first case, the cat was placed in a cold garden shed, and a lamp, which when illuminated provided some warmth, was either turned on or off, depending on the output of the binary random generator. There were 1000 tr ials in each of ten sessions. In the second case, cockroaches were placed on a grid through which shock was or was not delivered, depending again on the output of the binary generator. There was an exploratory series of 25 sessions, followed by a confirmatory series of 100 sessions with 4 runs per session and 64 numbers per run, all this preset. Randomization controls: In the series with the cat, these consisted of running the RNG for ~ hours per night for 24 nights, with the lamp outside, and the complete system left running. No bias was evident in these 691, 200 trials. Between sessions, we are told, the RNG was left running continuously to verify the lack of bias. In the cockroach study, the RNG was left running each night after PK test; again no bias was found. As additional protection against bias, both generator outputs used equal number of times to produce +l (shock) (The rep<,rt does not explain whether the reversal was made half way through the experiment, or at various times). Results: In the study with the cat, the first 5 sessions yielded above an average rate of +1's (lamp on) (CR = 2.421. However, the next five 75

(Alcock) sessions yielded results which were (insignificantly) below expect- ation. In the cockroach study, it was found in the confirmatory series, as in the exploratory series, that the cockroaches rece4ived significantly snore shocks than would be expected by chance (p < 10- ). Evaluation: These were very poorly deslOned and executed studies. Again, there were no short-term randomness checks.(Test sessions were only i/2 hour in length). It was not specified (or at least not stated) in advance that there would be 10 trials with the cat. On what basis were the first five separately analyzed and why was there no overall analysis of the ten trials taken together? Indeed, one cannot take the results of the first five trials, an arbitrarily chosen block, to be indicative of anything, especially given the results of the next five trials. Schmidt readily generates ad hoc explanations: during the second five trials, (for which the data were not significant), he comments that the cat seemed disinterested in the lamp. Would this same observation have been forthcoming had this subset of trials been significant? Further, Schmidt suggested that the reason that the cockroaches received more shocks than expected by chance may have been that it was his PK and not the insects' which was the psychic influence, and given his dislike for cockroaches, this led to excess shocks. However, he alluded to another experiment with cockroaches which ran automatically without the experimenter present and which produced similar results. He stated that these would subsequently published, but to my knowledge, they have not been. OVERALL JUDGEMENT: This study is clearly inadequate as a demonstration of anything having to do with psi. This paper would never have been accepted for publication in a mainstream psychology journal because of the methodological weaknesses and general sloppiness. Had Schmidt thought the results to ba as compelling as he suggests, one would expect to see a series of further studies of the same sort. That is not the case. Schmidt {1970b): "A PK test with electronic equipment": With this study, Schmidt, again the sole experimenter, switched from the four-lamp modulus-4 random generator to a nine-lamp binary generator. The generator produced a random sequence of +is and -is, based on radioactive decay.. The subject viewed a circular display of nine lamps, only one of which was illuminated at any given time. The random event (+l or - I) determined the direction of progression of successive illuminations. The subject's task was to chose a direction and then try to make the lamps advance in that direction. If the subject chose counterclockwise, a switch was flipped to make the lamps go that way on a +l, but a +l stilI registered as a at. 76

(Alcock) Randomization checks: Again, as in the earlier studies, success is demonstrated by the degree to which the correspondence between the subJect's goal and the outcome exceeds what would be expected by chance. Thus, it is of utmost importance to demonstrate that the random number generator is free of bias, and to this end, Schmidt generated 4,000,000 numbers on many different days (it is not specified what relationship of these days to experimental sessions was). The number umber of +ls, -is, and "flips" (i.e., a change from +1 to -1 or vice versa) was then examined, and no bias was detected. Schmidt, presumably showing sensitivity to criticism of his earlier experiments with regard to his having used control sequences which were much much longer than the target sequences, also divided the numbers into 10,000 sequences of 400 and looked at number of +l, -l and flips in each of them. The outcome of this was consistent with the normal dis- tribution. (However, it is not so much the overall distribution that is important here, but rather the sequences: Do a number of high 400 sequences occur in a row, for instance?) An additional measure was taken to protect against bias: after the first half of the confirmatory test, the two outputs of the generator were interchanged internally, so that any bias in favour of one digit would be reversed ~ we are not told what the breakdown of scores were before and after this change. Could it be, for example, that the deviation was highly negative pre-change, and only barely positive post-change, thus giving an overall negative score, but one much less impressive than in earlier studies (1969a,b)? Results: Although Schmidt ran some preliminary trials with i~ subjects, and reported and analyzed the data, such tr ials should be viewed only as pilot tests and not of concern to us here. In his "conf irmatory series", f if teen subjects took part. The number of trials was preset: there were 64 sessions of 4 runs each, with each run consisting of 128 binary numbers . Sub jects, as is typical in Schmidt ' s experiments, contributed varying amounts of data. No individual results were reported. Overall, there was a negative deviation of 302 hits, which was statistically significant (p<.OOl, 2-tailed). However, this is precisely what Schmidt expected! Negative scoring was indeed the norm in the preliminary trials, and this led Schmidt to predict negative scoring and to motivate the subjects to score negatively and to only use subjects who did score negatively in the preliminary trials; (all but one of those subjects did just that). Randomization checks: Schmidt reversed the outputs of the generator half way through and stated that if there was a systematic bias, this would compensate. However, no data are provided for the target sequence before and after this change. Also, while we are told that the randomization checks rule out biases, short-term biases are not ruled out by this procedure. Schmidt almost alludes to this himself when he discusses the possibility that the study might be tapping precognition (of the subject or the experimenter) rather than PK: 77

(Alcock) "Since the sequence of generated numbers depended critically on the time when the test run began, and since the experimenter, in consensus with the sub- ject, decided when to flip the start switch, precognition might have prompted experimenter and subject to start the run at a time which favored scoring in a certain direction." (p. 181} . Evaluation: Again, it is disappointing to see Schmidt change procedures without really having done more than a cursory investigation with the earlier ones. Here Schmidt switched to a binary generator (after having used his modulo four twice, and the Rand tables once). As well, because only one subject, in the preliminary sessions, really scored highly in a positive direction, it was decided that, for some reason, negative scoring was "intt, and so negative scoring was predicted for the "confirmatory" trials. The high scorer was eliminated and negative thinking was encouraged. The subjects who scored most negatively were used most in the confirmatory series, and new subjects were added only if preliminary testing suggested negative tendencies in scores. Why, how can the task suddenly become a negative one? Or is this all because that initial group of sub jects just happened] to be largely negat i ve? The subjects were encouraged to think pessimistically and in terms of failure. Yet Schmidt alluded in this paper to the notion that PK is goal-oriented- even in a complicated set of circumstances, results are obtained by concentrating only on the goal. Here the goal is self- contradictory: sub Sects were supposed to try to inf luence the lamp to go in the direction of their choice, but they were also supposed to want to f a i ~ ! Why not have them concentrate on havi ng the sequence go opposite to their preferred direction? It is actually worse than that; if the subject chose to try to make the lamps light in a counte r -c ~ ockwi se ~ ~ rect ~ on, a swl tch was f ~ ~ Sped to cause a + ~ numbe r to move the illumination of the lamps in counter-clockwise direction, so that failure (an excess of -Is), which is ready success (because sub] ects are encouraged to ps i -mi ss ), i s now ~ i nked wi th pe r ce i ved success on the board, whereas when the subiec~c chose clockwise, fa i lure (excess of -Is, again which is really success ~ is associated with per- ce ived fai lure on the board . What is the goal-directed PK going to do? An ef fort was made this time to prespecify the number of sess i ons and trials; however, the number of sessions Sicily varied between subjects. This is not a fundamental problem, but it indicates a certain sloppiness which is unwelcome in exper iments which are supposed to demonstrate the existence of a phenomenon which seems to defy the contemporary scientif ic worIOview. 78

(Alcock) OVERALL JUDGEMENT Again, much more work is needed to explore this situation to see Just what exactly is going on. Schmidt accepts his findings as evidence of psi and then simply moves on to something else. In my judgement, this paper, quite apart from its parapsychological nature, would not be publishable in any good psychological journal. Schmidt (1970~) "A Quantum mechanical random number generator for psi tests". No experiments are reported here. This paper presents a description of Schmidt's binary RNG and a discussion of his randomness checks. Schmidt & Pantas (1972): "Psi tests with internally different machines". This study was designed to try to differentiate between precog- nition and psychokinesis in a psi task. Subjects used a test machine which involved choosing which one of four lights would be next selected by the random event generator . I n the precogn i ~ i on mode, the machine worked just as in the ]969 studies; pressing one of the four buttons activated the random event generator and one of the four lights subse- quently was lit. In the PK mode , the ~ i ght correspond i ng to the de - pressed button lit up, indicating a hit, only if the internal generator produced the number 4 ~ from amongst its range of I, 2, 3, and 4 ~ . Thus, only by psychokinetically forcing the production of fours could the sub ject increase the hit rate . ~ Schmidt admits that these are not pure precognition or PK modes, for PK could be involved in the precognition mode to influence the generation of a number corresponding to the button depressed, and i n the PK mode, one could use precognition to wait until the chances for obtaining the desired target were good). The mode could be changed by a flip of a switch, but the subject would be unaware of any change, since the task as presented to the subject was identical for the two modes. First experiment: In the first experiment, the goal was not psi-hitting, but rather, psi-missing. Schmidt tells us that, "Psi-missing had been observed in preliminary tests in which the subject had to perform in front of a group that reacted with friendly laughter to each of the subject's misses" (p.226) . One might well wonder what would motivate Schmidt to create such ~ test situation: Schmidt tells us that the subject was instructed to try to miss rather than hit, and so the goal was psi-missing. Thus, the 79

(Alcock ) negative inf luence of the laughter UpOll the sub ject t S misses ( which are, in this case, successes) then pushes the subject towards more hits (which in this case are failures, or misses). Thus, the interpretation given to the above chance hit rate is that the subject whose goal was psi-missing actuail,y "psi-missed" that goal, producing psi-hitting! It 's not clear Just exactly how the decision to study psi-missing in this experiment came about. (Were the three pilot groups actually asked to avoid hits? It seems so, since Schmidt says that the usefulness of this procedure was suggested by their results, and since they scored above chance then it would seem that they had not been instructed to L~ to score above chance. But why would he ask people to psi miss in the first place?) Schmidt ignores a logical morass which is created by his two-mode precognition-PK machine. In the precognition mode, all is well: if precognition exists, the subject foresees what light will light next and then presses the corresponding button. Alternatively, if PK is used, the subjects could supposedly arbitrarily choose a button and then exert psychic pressure to cause the corresponding lamp to light. In the PK mode, however, things are different. If the subject only uses PK, then he or she must learn that success occurs only when 4's are generated, and then the subject must bend his/her psychic influence to produce more 4's. Consider, however, what would happen if a subject tried to use precognition in the PK task. (Note that the reason Schmidt calls this a PK mode is because it would be difficult to succeed merely by precognition). It is more than merely difficult: it leads to such logical confusion as to put the possibility of precognition into question. If precognition involves seeing what light will light next, and if one presses the button beneath that light, then if another light lights because the random generator did not produce a four, one did not foresee the right light. Suppose precognition were perfect: one would know then which button would light up, but if one presses the button for that light, unless one is somehow constrained to wait for a 4, one would be defeating the precognition. Schmidt was the primary experimenter in the first experiment, but in most tests, we are told, a second experimenter (one of five people) was also present . Sub jects consisted of 18 groups of students, teachers, etc. whose participation usually followed a lecture on ps i; the test ing was done outs ide the laboratory ~ presumably at the place where the lecture was given ); although we are told in the introduct i on that the machine allows switching back and forth between modes, " f or practical reasons " each group worked in only one mode . The mode was switched for each subsequent group. Only the principal experimenter, Schmidt, knew that the exper iment included two types of tests . The r e was a total of 214 subjects in the precognition group and 157 in the PK group; there were varying numbers of sub jects per group, and data i s presented for groups, not individuals. It ts an example of tI~ sloppiness of the preparation of the report that one only discover s when one reads a footnote to the table of results that each ind ividu.a 1 80

(Alcock 3 participated only until he or she obtained a hit. Only 500 trials were planned for each mode, but 740 trials were run in the precognition mode (another dl~quieting indicator of methodological sloppiness), and so the last 240 -were not used in the analysis. (My check shows this does not work in favour of Schmidt's hypothesis; his results would be stronger if he had left the 240 additional trials in). Randomization checks: None described. Results: The scoring rate in the precognition mode was 29.B%, significantly higher than the 25% chance level (p < .0l, one-tailed). In the PK mode, the scoring rate was 31.4`, again significantly higher than the 25% chance rate (p < .0005, one-tailed). Second experiment: Schmidt was the only experimenter in the second experiment, which involved only one subject, co-author Pantas. After a pilot test 500 precognition trials were run followed by 500 PK trials; these were run in blocks of 25 per session; usually ~ session per day. Pantas first was tested in a precognition pilot test (350 trials), and then a "confirmation" precognition series (500 trials), and finally a "confirmation" PK series (500 trials). Pantas was left alone with the machine for 20 minutes to practice Zen before each session. Schmidt was not present in the room, but by monitoring the paper punch "could follow the progress of the test whenever he wished without disturbing the sub ject" (p.231~. Randomi zat i on checks: None descr ~ bed . Results: Pantas scored at about the same above-chance rate in all three series, including the pilot (pilot, 30.9`, significant at p ~ .01; precognition, 32. By, p < . 00005; PK, 30`, p < . 005, all levels one-ta i led 3 . Evaluation: No mention was made of any randomness checks in these two studies, but one would presume that Schmidt must have carried out the same kind of inadequate control runs that he carried out for earlier studies. Obviously, the above-chance scoring rates are only of interest if one can be certain that there were no biases in the target series. Again, the Hansel control procedure ~ i.e., taking target runs two at a time and randomly assigning one to the exper imental ser ies and the other to the control series ~ would be invaluable. It would be of considerable interest to examine the actual target series used in the various tests. For example, if PK is actually being used to produce more 4's in the PK series, one might expect that the PK target series would include more than 25% 4's (as was apparently the case, given the approximately 30% hit rate I, while one might expect that this would not occur in the precognition series, where there would be no need] for it. On the other hand, if one found a similar excess of 4's in the precoq- nition series, this might well tempt one to disbelieve that PK had been 81

t Alcock ) at work in the PK ser ies . Indeed, it is interesting that Schmidt arbi- trarily chose 4 as the number to force in the PK tests, for one of his subjects in an earlier study had reported that he had tr fed to generate more 4's (going against the instruction to try to predict which lamp would next light up), and Schmidt found more 4 's in his target series. The skeptic might suggest that Schmidt's machine is prone to a short-term bias which boosts the production of 4's. One would like to examine the subjects' responses in the precognition series, for if they obtained their above-average score rate through "response-matching", one would expect that they would have learned to depress 4 more often than the other buttons, and one should see this in their responses. On the other hand, the PK set-up dId not allow for response-matching, and the subject could hit any button and still obtain an above-chance score of 30` as long as about 30` of the target numbers are 4's. Again, there were no controls; one would like to see, for example, half the subjects attempting to demonstrate psi-hitting, and the other ha l f ps i -mi ss i ng . Howeve r, Schmidt mi ght we ~ ~ argue, as he s ugges ted in the introduction, that these Ss for whatever reason were more attuned to ps i missing. This is unsatisfying. Note that f or the f i rst exper iment there was no paper punch; yet this is probably not why Schmidt ran the system only in one mode or the other f or any g iven gr cup, rather than switch) ng back and f orth without the sub jects' knowledge. The paper punch probably did not record the mode, for although it was used in the second experiment, which used only one subject, all the precognitive trials were run and then all the PK tr ials; ~ Does this not mean that Pantas could have changed back and f orth between modes had he wanted to, wi shout E knowi ng, ~ not that th i s s hou ld mak e any cl i f f erence ~ . At any rate, the pr ocedure i s ce r ta i n ly vulnerable to recording errors since the recorcting and computations are not automated. (?\rERALL JUDGEMENT: Once again Schmidt has served up an empir ical report where he makes a number of shifts from earlier studies: a new mach i ne arrangement, test i ng carr i ed on outs ide the laborat ory, wi th no paper punch to record results, at least f or the f irst exper iment, double psi-missing as the goal (the subject, whose qoal is to psi-miss, is actually treated in a way that might lead him or her to psi-miss tI~e psi-missinq, thereby yieldinq psi-hittinq); a subject continues until he encounters a hit (i.e., really a miss) and then his participation is over. Not only are there these changes, but there are some flaws from earlier studies which remain uncorrected: the randomization check ~s the most serious of these. The fact that a co-author serves as the sole subject in the second experiment makes one uncomfortable as well. Again, quite apart from the parapsychological nature of the paper, it is my judgement that it would not be accepted for publication in a good psychological journal in its present form. 82

( Alcock ~ Schmidt, H. ( 1973 ~ "PK tests with a high-speed random number generat- or" . In this research, Schmidt examined PK using a two-speed fast REG driven by electronic noise (since radioactive material manifesting high-speed decay was not available). Schmidt suggests that a high speed REG might increase efficiency and allow subjects to identify states of optimal psi readiness and then learn to cultivate these states. An exploratory study, involving four subjects, including Schmidt himself, were run. Because of the exploratory nature of the study, those results wi ~ ~ not be ~ iscussed . In the "confirmatory" study, there were ten subjects, including Schmidt, chosen from a pool of subjects. Subjects were given feedback following each run; and sub jects chose in advance to take the ir feedback in either a visual or an auditory mode. In the former, feedback was in the form of the deflection of a lO-pen recorder, and the sub ject 's task was to attempt to get pen to go in the target direction. deflection from the midline indicated cumulative excess of hits over misses; momentary movement indicated momentary scar ing rate ~ . In the auditory feedback mode, feedback was in the form of clicks in a pair of stereo headphones; a click to one ear indicated a hit while a click to the other indicated a miss. There were two presentation speeches, either 30 events per sec (run= 100 in confirmatory study; duration about 3") or 300 per second (in which case a run consisted of 1000 events in the confirmatory study, and this took about the same length of time as for the slower speed. When both speeds were used, the speed alternated from session to session. In the visual condition, the subject could not discriminate speed, and no effort was made<to inform the subject unless the subject asked. All three visual feedback subjects participated in both fast and slow conditions. In the auditory condition, one could discriminate between fast and slow, and so subjects were allowed to choose their speed; two chose the fast speed, four chose the slow speed, and one (Schmidt himself ~ chose to work with both speeds. Etandomi zat i on contr ols: The generator was le f ~ unat tended f or ~ ong periods, usually overnight; the numbers of binary ~ 's and O 's were counted, as were the number of flips. Schmidt indicated that, "Depending on whether the experimenter had set the + l or the -l as the goal, this number were shown in the display as a "hit" and the other number as a "miss"" (p. 108! Schmidt said that each goal was used equally often. No indication is given of whether or not the target was alternated from session to session - or whatever; in any case this would not change the bias problem. 83

(Alcock) The report states that the subject's momentary efficiency was frequently rechecked in warmup cons before they were allowed to contribute to a test session. Security. unspecified; tt is not. clear if the subject was alone with the apparatus during the testing. Recording: In the confirmatory series, recording was done manually, but in addition, it was also presented on the pen recorder (visual feedback), or tape recorder (auditory feedback) which allowed for later rechecking. Both procedures, however, allow recording errors. Results: In the confirmatory series, it was decided in advance to complete 200 runs under each of the four conditions (auditory slow, auditory fast, visual slow, visual fast). Individual subjects, as is typical in Schmidt's work, contributed various numbers of trials. The combined results (hit rates) were as follows: slow fast visual 51.9 50.36 auditory 51.4 50.39 All four hit rates are significantly different from zero. (Although multiple z-tests are performed, the z's are so high that one need n`'t worry about the effect of multiple testing on the Type I error rate d. There was no significant difference between visual and auditory modes, but the hit rate was significantly higher with the slower rate of target generation. This is consistent with the notion that periods of short-term bias were selected by the immediate testing prior to each tes t tr ia ~ . Evaluation: Schmidt found that subjects performed more poorly with the fast rate of target generation. This is consistent with notion that successful subjects might owe their success to exploitation of short-- term generator biases; since subjects were given repeated pretests before each test session to insure that they were in a good ps! state, then, presumably, if one does not beg the question and assume that ps i is in operation, the indication that the subject is in a good psi state is equivalent to an indication that a period of short-term bias has been encountered. Suppose that the average length of a "biased" portion (perhaps a warm-up effect) of the target series is N targets, regardless of speed of generation. In the slow speed, the sub ject is exposed to 100 targets per run and, in the fast speed, to 1000 per run. Therefore, the subject, if there is a bias, is likely to run over that bias in the 1000 number run and get a percentage of hits that i_ lower . In the fast speed of 300 per second, it also means that the t inane taken between pretest and test may "use up" more of whatever momentary bias exists. 84

( Alcock ~ OVERALL JUDGEMENT: Agair`, because of the fact that the entire claim for anomalousness lies in the departure from randomness in the target series, one cannot accept the results of this experiment as indicative of an anomaly because one cannot be certain that the results are anything more than the consequences of a random generating system with short term biases. In addition' one might add that once again, Schmidt is sloppy in his arbitrary assignments of subjects and in using himself as ~ sub ject,, setup ity measures are . · . ~ ~ not discussed in this paper, recording errors are possible, and, finally, the report is rather poorly written. It would not be accepted for publication in any good psychological journal, quite apart from its parapsychological nature. Schmidt. H. (19741 Comparison of PK action on two different random number generators. Here, Schmidt's idea was to use two different REGs, one simple (binary, driven by radioactive decay) and the other complex (strings of 100 binary digits are generated rapidly and if a string contains an excess of +l's, a +] target is generated, while if there is an excess of -l's, a -l target is generated. (No target is generated in the case of a tie). The sub ject sat facing two lamps, one marked "heads", the other "tails". One or the other was the target on a given trial (although we are not informed as to how this decision was made I, and so the sub ject's goal is to try to have that lamp light up. Once the sub ject act ivated the tr ial , a random process connected one or the other of the two generators and then, depending on the generator output, one or the other of the lamps was lit up. The subject was provided with continual feedback via a pair of counters indicating number of trials and number of hits. As usual, Schmidt was the sole experimenter . There was a pi lot study in which four subjects, including Schmidt, participated. In the "confirmatory" series, there were 35 subjects, again including Schmidt himself. The subjects were divided into three groups, fir "sections": groups ~ (five subjects) and 2 (ten subjects) were composed of members of the parapsychology institute where Schmidt worked, as well as of others who had previously shown good scoring rates. Subjects in the first group knew the goal of test, while those in the second group, with one exception, did not. Group 3 was comprised of twenty visitors to the institute who, in a short preliminary test, produced good scores. It was decided in advance to run 1000 trials for each group. (Actually about 10% more were run for each group, but this apparently did not affect the outcome). Therefore, each subject ill group ~ was do about 200, in group 2 about 100, and in group 3 about 50. (One must ask why these figures were approximate rather to prespecified and exact). Subjects were allowed to make their responses over one or a number of sessions. Sessions were frequently interrupter by coffee breaks, walks on the porch or conversation, at the subject', 85

( Alcock ) whim. Note that there is no indication of why the number of trials per subject vary so much, or how it was determine] when to stop a given subject. Presumably, given that the subject could interrupt or stop the session at any time, it was stopped by the sub Sect ~ or experimenter? ~ whenever he or she felt like it. Again this is a problem i f there are short term biases in the generator output . Randomization checks: None were mentioned in the report. The recording of output form the S generator when it was inactive presumably serves as a control, but Schmidt does not suggest this. The determination of whether or not S or C would be active was determined by a random ser i es recorded in a prepunched tape. Recording: A pen recorder was used to record (a) which generator, S (simple) or C (complex), was active; (b) the output ("head" or "tail") of the active generator; (c) the output of the S generator when it was the inactive generator, and (~) the target side (i.e., left lamp or right lamp). Note that the number of hits not automatically recorded but had to be calculated by hand from the pen recording or read from the counters and then pr ocessed . Security: The experimenter was in the room with the subject, but did not look at lamps; recording and generating equipment one floor down. (Was it seen over by someone else? The report does not say). Results: In the confirmatory series, statistically significant PK effects were found for both generators, and there was no significant difference between them. There was no indication that some subjects were more successful than others. No PK effect was found for the S-generator when it was not in active use. Overall, the hit rate was 55.3% for the S-generator and 55.3` for the C generator. The S generator when not In active use produced a hit rate of only 50.7, not significantly different from the 50% chance rate. Evaluation: Several errors in text and tables make for difficult reading. That aside, there are a number of concerns: 1. It is unfortunate that Schmidt viewed the recording of S-inact~ve only as a way of checking for displacement effects; had he recognized its potential as a control, then no doubt he would also have recorded the output of the C generator when it was inactive, and he would thus have had a control procedure very close to what Hansel has called f or - a pair of random events for each trial, and a random selection of which is the target and which is the control . Why was not the output o f C recorded when it was inactive? We know from earlier studies that Schmidt has a ten-pen recorder; it seems bizarre that he should not record C-inactive. Did he choose not to report it? 2. In approximately half of the trials in each session, the "head" lamp was the target, and the "ta i l't lamp was the target for the rest . No 86

(Alcock) indication is given of how this choice was made. If the choice was random, then there should be no problem, but i f there was a long sty ing of one lamp as "head" followed by a long string of the other, this allows the possi})i].~ty of short-term generator bias to be a problem. However, the lack of above-chance scores for S-inactive apparently null i f ies this concern . 3. Again, as seems typical with Schmidt, there was considerable sioppi- ness in allocation of sub jects and tr ials . As in other of his exper i - ments, Ss are chosen from a larger pool on the teas is of success in preliminary tests. (How are we to be certain that no data was eliminated after the fact? This is a temptation to every graduate student: "Gee, Smith's results throw the whole thing off - but then, he did say he had heard somebody mention having been in the experiment, so he wasn't really naive, so we cannot really count that!"3. As usual, Schmidt combines varying numbers of trials from various subjects. This time, having preset the number of trials per group at 1000, and stating that each subject would participate in about 200 trials, it turns out that the range in the number of trials per subject in Group ~ was from 195-263, while the range in Group 2 was 99 to 125 (when about 100 each were planned) and in Group 3, 27 to 124 (where about 50 each were planned. Again there is the worry that this makes exploitation of short-term biases possible; after all, the subject has continual feedback, and can start and stop apparently at whim. OVERALL JUDGEMENT: Because of the presence of the scores for S-inactive, these data carry more weight, in a sense, than previous data. However, one would wish, before concluding that a genuine anomaly is occurs ing, to redo the study recording both generators when they are inactive, and tak ing steps to ensure that there is no post-hoc elimination of subjects. One would like to see a Schmidt-type experiment with equal numbers of subjects in the var ious groups, with each contr ibuting the same number of trials, with no feedback, and with adequate controls (using the Hansel-Hyman procedure ~ to protect against short-term bias. Since Schmidt would no doubt argue that all but the last of these would vitiate conditions necessary for the subject to remain relaxed and well-motivated, I would settle even for the last of these measures, f or it is by far the most important. once again, because of the lack of adequate control procedures, one cannot take the results of th Is exper iment as evidence f or tile existence of an anomaly. Once again, then, this paper would be unlikely to be accepted for pub! ication in a good psychology journal, quite apart f ram its parapsychologica~ nature. 87

(Alcock) Schmidt, H. (1976) PK effect on pre-recorded targets. With this report, Schmidt shifts his research direction towards the study of retroactive PK effects. The basic idea was to see whether or not a subject's PK effects could influence a series of randomly generated events that were generated in the past Three experiments are reported in this paper. First experiment: The first part of the first experiment is a conventional PK experiment, using an electronic random generator with p = I/64, q=63/64. For each test, the generator was automatically ac~clvated at the rate of 10 trials per second until a hit was obtained, and then the generator stopped, and hit was indicated to S as a weak click in earphone. On average, it should take 64 trials before a hit is obtained, if only chance is operating. The second part of the f irst experiment was the same as this, except that the PK targets cons isted of a random sequence o f h i ts and misses generated and recorded on audio tape earlier in the absence of sub jects and exper imenter . No one saw or heard the sequence unti ~ it was played during the experiment. One-half of the sequence was used as the target, while the rest was used as a control and analyzed directly by the computer: A first sequence of 60 runs was generated and labelled A; a second sequence was generated and labelled B. Ten such pairs of sequences were generated. A randomizing procedure was followed to determine whether or not A or B was used. After the first A, B pair was generated, the first subject was selected and tested. After three such subjects were tested, this procedure was repeated : a new A, B pair of 60 runs, 3 new Ss selected, etc. Results were computer evaluated from paper tape . Sub jects were given cumulat ive feedback immed lately after a sess ion . Conf irmatory study: Sub jects compr ised a prespeci f fed number of laboratory visitors (30~. Each subject participated in one session of twenty test runs each, run as two sets of ten runs each with a lO-minute break in between. Recording: The equipment was set to run automatically once started, and data recording was automatic. Randomness checks: Schmidt reports that randomness tests between sess ions were cons istent wi th ache theoret ice ~ ly expected average r un length of 64. It would appear that the control and test runs were of the same length . THe conclus ion about the lack of bias was based on 4000 runs Results: In the f irst part of the study (real-time i, the average we i t for a hit was 55. 34, slgnlficantly lower than what was expected by chance . In the second part of the exper iment, us ing prerecorded target sequences, there was also a significantly reduced run length of 56. 37. 88

(Alcock) Indeed, the results were pretty much the same regardless of whether targets generated in past or present, which is not inconsistent with the possibility that all the results are due to artifact. Second exper iment: Here Schmidt used a fast binary random generator which produced sequences of heads/tails at pitcher 30 or 300 per second (as in Schmidt, 1973 ~ . The sub ject was given both auditory feedback (variable frequency sound, the goal being to lower frequency) and visual feedback in the form of a fluctuating display needle, (the goal being to move the needle to the left). Twenty subjects chosen from a pool of thirty volunteers each contributed two test runs, carried out in a single session. Each run consisted of 4 sequences, and each sequence comprised 256 binary digits. Two types of targets were used: the target alternated between a "momentarily generated" (or "real-time") target and one from a prerecorded ser ies. There were 4 target sequences of 2S6 binary bits ea ch; the ~ 2 ~ odd -numbe r ed tar Be ts were taken f r om a pr ede te rmi ned random sequence stored in the computer memory, while the 128 even-numbered ones were provided by triggering the binary random generator. However, while the momentarily-generated targets were freshly generated each time, the same prerecorded series was repeated in the same order in each of the four sequences. Following each sequence, there was an intermission of 15 seconds during which feedback was given. Recording: Recording was automatic. The number of heads and tails was recorded in paper tape before and after runs to ensure contents of memory not altered psychically ~ That would be strange; but Schmidt must think that it is easier to go back in time and affect quantum processes than it is to alter the data stored in a computer ~ . Randomness checks: There were f ive control runs before and after each test session; on each run, 128 numbers were generated, stored i n memory, retrieved and recorded. Over the 200 control runs, there were 12, 715 heads and 12, 885 tails; the CR=., which is race signif leant). As an additional control measure, the target side of the generator was alternated on each session in order to protect against a constant bias. Results: Compared to a chance rate of 50%, the hit rate for momentarily generated targets was 50. 8iS (p < . 05 one-tailed), while for prerecorded targets, it was 52.95% {p < .0005~. Schmidt concluded that repeated feedback of prerecorded data Te aid., to increases in scoring rates: the within-sub jects difference between prerecorded and momentar i ly generated was s igni f icant . He assumes t}; i t the superior rate obtained for the prerecorded] targets was due to r ~ - peated presentations. 89

(Alcock) Evaluation: Again, there is reason for concern about the adequacy of the randomness checks; the Hansel procedure would control for short-term biases; the procedure followed here does not. Third experiment: In this experiment, there were two binary random generators, one, the "difficult" one, with P(hit)= I/8 and the other, the "easy's one, with P(hi4~= 7/~. These two were activated in a random sequence so that subject never knew which would produce the next targ- et. In the pilot study and in the first half of the confirmatory series of this experiment, feedback was presented in the form of clicks to the left ear (hits) or right ear (misses) via stereo headphones. Then, and no reason for this is giver., the rest of the confirmatory series employed auditory feedback which took the form of either a high or a low tone. The random order of presentation of generators was determined by prerecorded random sequence of 64 binary digits ~"heads" and "tails" produced by a ran<3om. generator ~ having P ~ head ~ = P ~ ta i ~ ~ = ~ /2 ~ pr i or to the exper iment: a head led to the use of the 7/8 generator, whi le a tail led to the use of the 1/8 generator. Since more heads lead to increases in the total score, there should be motivation to want the 7/8 generator, and this might lead the subject to influence the prerecorded sequence by means of PK. Each sequence of 64 binary digits was used 4 t imes i n succession, so that each head or tail caused four triggerings of either the easy or the difficult generator. There were forty sessions in the confirmatory series, and each of these consisted of four test runs; each run involved 64 random events, and feedback was given after each run. Twenty-eight volunteers participated, and some of these performed in up to three sessions because of a shortage of volunteers. Results: While the pilot series seemed to support the existence of a PK effect, Schmidt said, the effect in the confirmatory series was only "marginally signif icant" at the .05 level. (Note: the abstract says that PK effect on prerecorded sequence was confirmed at the .05 level. Yet, the l-value is only l.3; this is only the .10 level o~e-tailed! However, Schmidt also provides a CR (z-score) of 2.03 and this is presumably what he refers to as "marginally significant at the . 05 level . He only gives the l-level in the table; why has he been us ing ts instead of Zs, and why does he only refer, it seems, to the Z in the abstract? Why does he use both z and ~ in the table for the first experiment?) Evaluation: The third experiment was a failure; apart from ~ significant deviation in a pilot series, there is nothing, Schmidt'= born-again CR not withstanding. ~y3~L ~9~, These are the most automated and least sloppy of t~= studies so far. The number of subjects and number of trials w-~- prespecified; automatic equipment operation and recording was used. 90

(Alcock) Contorl runs appear to have been of the same length as test runs, and were interspersed with them, although it seems that the decision that there was no bias was based on the overall set of control runs for a given experiment, and no attempt was made to check for trends that might cancel each other out, but still give short-term biases which could aid the subject. Oddly enough, just as this wr iter begins to be more contented with the procedures (although not yet persuaded that biases in the random sequences have been ruled out; the Hansel procedure would be desirable for that purpose ), Schmidt begins to sound more conservative: "With any interpretat i on of the results one has, of course, to be cautious for several reasons. First, one mi ght want to postpone ser i ous ~ i scuss i on unt i ~ we have more detailed experimental information from several independent exper imenters . Second, the failure of the third experiment to give more than a marginally signif icant PK effect reminds us that we may still be overlooking some vital factors which have a stronger ef feet on the test results than the variables we are studying. . . " (pp. 290-291) . I concur. Schmidt, H. ( 1978 ) A take-home test in PK with pre-recorded targets . First experiment: The basic idea here was to generate, using a binary random generator, a sequence of tones on an audio tape, the pitch growing successively higher for each hit and lower for each miss. Each run comprised 512 binary events, and there were twelve runs per tape. A random assignment procedure was used to categor ize each tape as either High or Low. Then the subject would take home a copy of the tape, and as he or she listened to it, the attempt was made to increase the tone, if the tape was assigned to the high category, or to decrease the tone, if the tape belonged to the low-category. Subsequently, Schmidt, again the sole experimenter, would evaluate his copy of the tape for imbalance between the numbers of hits and misses. Actually, he examined a computer printout of hits/misses prepared at time tape was prepared, but which had not viewed until after the subject had finished his task. (Thus, this printout was, effectively, tile data). There were twelve runs each of High and Low, and each run consisted of 512 binary digits. Second experiment: The second experiment was similar, except that, whereas in the first experiment, the 10 subjects were able to play around with the machine before taking home the prerecorded tape, in the second, 64 volunteers were contacted by telephone and the tapes mailed out. In addition, half the runs were "group" runs, in that four different subjects received identical recordings; the other half were 91

(Alcock) individual runs.(One side of each subJect's tape was an individualized series, while the series on the other side was sent to three other subjects as well. Further, for half the subjects in the individual and group tests, the printout data were seen by an assistant, who did not know their meaning, before the subjects made their PK efforts. There were twelve individual runs and twelve group runs; half of the runs in each condition were low and the rest high. Thus there were 64 individual runs and 16 group runs for a total of 80 runs. Randomization checks: None were reported at all for the generation of the tapes. Recording: No data needed to be recorded. All that was required was to analyze the original computer printout for departures from randomness. This was presumably done manually. Results: For experiment I, all we are told is that the CR = 3.34, (p < .0011; no data are presented. We are also told that a t-test on the 10 total scores (comparing each subject's scores for high and low tapes) yielded a t = 0.86, 9 Of. This difference score was nonsignificant. There were no significant findings in experiment 2. However, Schmidt reanalyzed the data and found that the squares of the CRs (critical ratios), (in effect. z-scores squared) were all were above the chance level of 1, and this is taken to suggest a combination of PK h i tters and missers. Combining all CR-squared ~ ~ O contr ibut i ons ~ g i ves an average CR-squared of l. al, p=. 03, only "suggestively high". Evaluation: No data were provided in this paper, just test statistics. Although a significant effect was found in the first experiment, the second really serves as a failure to replicate, al- though, because of the changes in procedure, Schmidt takes the outcome to suggest that the informality of sending out the tapes by mai ~ in some way decreased the likelihood of psi. The absence of randomization checks None were reported ~ by itself would render this paper unacceptable for publication in psychology Journals. Terry, J. & Schmidt, H. (1978). Conscious and unconscious PK tests with Prerecorded targets. This study is a follow-up to the previous one, and this time subconscious as well as conscious PK efforts were under scrutiny. There were two experimenters involved. There were three separate experiments of 20, 20 and 30 sessions respectively. In the first two of these, there was a different subject for each session, while in the third, all subjects participated in more 92

(Alcock) than one session, and indeed some worked simultaneously on the same PK task. For the "conscious" runs, high tones were presented at random time intervals and the subject's task was to increase the number of such sounds. For the "subconscious" task, high and low pitched sounds were presented at random time intervals, and the sub ject 's task was to react to hi gh pitched sounds by press ~ no a switch as quickly as possible, but not reacting to low-pitched sounds. It was expected that the intense concentration on the sounds might lead to subconscious PK ef forts to shorten the interva ~ between success ive sounds . One experimenter used a randomization routine on a pocket calculator to decide which of two tapes would be used as an experimental tape and which as the control. Without knowledge of this decision, the other experimenter, Schmidt, prepared a pair of digital cassette tapes, each containing six sequences, corresponding to six runs, of random numbers. THe numbers were 0, i, and 2, chosen so that the relative frequency of 0 would be 15/16, while the relative frequencies of 1 and 2 would be 1/32 each. For the "conscious" runs, the i's produced a high tone, while for the subconscious runs, the i's and 2's produced high and low tones respectively. The control tape was not examined until the end of the experiment, at which time it, along with the exper imental tape, was read and analyzed automatically by a computer. The authors presented the combined results of the three experiments, and the only signif icant results were as follows: there was ~ igni f icant PK miss ing ~ p < . 005, 2-ta ~ led ~ in the consc tous runs, as well as a significantly high variance for those runs (p < .005 1- ta i led ) . There was not a s igni f icant di f ference between the 70 conscious PK sessions and the 70 corresponding control sessions. However , i t was found that the control sessions were b iased towards a smaller number of high tones, although the bias was non-significant. The authors added, "This non-significant bias, which also appears in the subconscious runs and the corresponding control runs, raises the question whether perhaps the random generator was biased, An extensive randomness test at the completion of the experiments, however, indicated no such bias" (p. 40~. Yet , age in the randomness test was one hundred times longer than the length of the series generated and recorded on the tapes. Evaluation: In this experiment, even the experimenters suspect non- randomness of the generator. Given that they were prepared to accept psi-missing as well as psi hitting as evidence of PK, all that was 93

( Alcock ) necessary to produce a significant effect was to initially generate two tapes that dif fered in some way because of generator bias . That is prec ise ly what appears to have happened . This study would not be acceptable Ear publication in a good psychological ~ ournaI, quince apart from its subject matter . Schmidt (1979a). Search for psi fluctuations in a PK test with c:ockroac:hes . This is a brief report in which Schmidt suggests that the reason that cockroaches were unable to avoid shock in his 1970a study may be that they do not encounter such shocks in nature and therefore have no preparedness to avoid them. By using random delivery of shocks at two different probabilities, one might have a more sensitive measure of their PK abilities, he argued, and by using repeatedly the same recorded series of events, again this might aid the cockroach in coming to be able to reduce the number of shocks. He thus compared the actual shock rates when the a priori probability of a shock was 1/4 against when it was 3/4. No eviednece for PK was found. Presenteing the same series of recorded random events 32 times did nothing to improve the avoidance of shocks. He also reported in brief his failure to find PK effects in studies with algae, yeast, and wingless fruit flies. Schmidt. H. (1979b) Use of stroboscopic light as rewarding feedback in PK test with pre-recorded and momentarily- generated random events. In this study, subjects attempted to affect mentally the duration of time intervals determined by random processes. The length of tile first part of each interval was determined in advance of test; tale second part was determined at the time, so that prerecorded an`] momentarily generated random events were both involved, and the mail goal of the study was to compare the two with regard to PK effects. During ON intervals, the subject was exposed to a strobe light flashing at a frequency which he/she had preselected as beiges particularly pleasing, while during OFF intervals, the subject viewed ~ practically constant light source. The subject was instructed to try t`: lengthen the ON intervals and shorten the OFF intervals. A test run consisted of ~ ON and ~ OFF intervals. Each t: rare interval, ON or OFF, had two sections; each section was n units (a ur,it = 5/16 seconds) long. Before a run' 16 random numbers were generated by means of an electronic die (based on radioactive decay): the rar;dc!r, number n was determined by the number of "rolls" of the electronic I] ~ before an 8 came up. The second part of each interval determined our_ 94

(Alcock) the run: the electronic die was activated once after every time interval during this run, and the section was terminated when an 8 appeared. The subject could not sensorially distinguish between momentarily generated and prerecorded sections. There were 200 test runs ~ i`'ided amongst the 12 sub jects . The report does not ind icate whether or not sub jects were g iven feedback. Subjects f irst made one or two unrecorded trial runs; if they still felt good about the test, they were then allowed to contribute to the test runs. When a subject returned for another session he would always begin with one or two warmup runs after which it was decided whether test runs should be undertaken or not. Random~zati on contr ols : noise ment i oned. Security: not stated. Results: No data were provided, not even means; we are only told that the observed ON inter`,als were seven percent longer than would be ex- pected by chance, and that this is statistically signif icant ~ CR = 4.26 ~ at the p < .0001 level . The OFF intervals were a non-significant 0. 5% shorter than chance expectation. There was an equal ef feet on prerecorded and momentar i ly generated intervals (6.~`, CR=2.9, and 7.3 %, CR=3.l, respectively). So, both prerecorded and momentarily generated ON intervals showed the effect, but there was no effect for OFF intervals. Evaluation: No data or discussion is offered regarding randomization tests; based on past history, one must suspect that there were no checks for short-term bias. Te warmup procedure, whereby the decision to proceed to test trials depended on the results of the warmup, furnishes an excellent opportunity to select for short-term bias if it exists. Given that data are not reported, even in summary f arm ( means, variances I, one obviously cannot evaluate the data. We do not even know how the 200 test runs were divided amongst the 12 subjects, except that it had to be unequally. Did one subject have a number of runs in a stretch and contribute disproportionately to the data? We cannot know. Note that if it is a question of bias, the ON and OFF intervals were interspersed; why should the bias only affect the ON trials? That is why we should like to see the data for each subject, to see war or not there is a pattern: did all subjects, for example, show an increase in ON length but not in OFF? OVERALL JIJD~HENT- This study is too sketchily presented to be able to evaluate +~e evidence in any meaningful way. It was a conference paper, which 95

~ Alcock ~ accounts no doubt for the lack of detail, but as far as I know, it has not been pub] ished in any other f arm. However, it seems that the same procedure which allows for selection of generator bias and which has been criticized in the discussions of some of the earlier studies was in operation here. ~ ~ wou ld not be pubI i s habI e i n a good psycho ~ ogy ~ our na I, qu i te apart from its theme. Schmidt, H. t1981) PK tester with pre-recordtd and pre-inspected seed numbers. In this research project, Schmidt addresses the question of what would happen if instead of using individually generated random numbers, one uses a causal algorithm which begins with a randomly generated seed number? Will there still be a seed effect? If so, does it matter if a human observer sees the seed number in advance of the test? Each run cons isted of 512 target numbers which were generated by an aigor ithm which used a seed number der ived from a truly random process. Seed numbers were obtainer] in advance, and half of them were inspected by the experimenter; ~ ". . .theoretically, the experimenter would have been able to calculate f rom the seed number the PK target sequence and the final run score" (p. 88) ~ . The task involved a circular series of 16 lamps in which only one lamp is lit at any given time. Random number generation worked on a modulus 16 basis, and with each generation of a random number, the light moved in one step either clockwise or counterclockwise: it would move clockwise until a 3 occurred, at which time it would begin to move in the opposite direction for each number generated unti ~ a 12 was obtained. This process continued until 16 clockwise-counterclockwise pairs completed. The subject's task was to try to make the light move clockwise. (There was an inverted switch which the subject could use if he/she wanted to make the light move counter-clockwise; the switch simply interchanged clockwise and counterclockwise movement in the display). Auditory feedback was also provided via a decaying gong sound which was on as long as ~ ight was moving in clockwise direct ion . The random generator operated as a 16-sided die, and left on its own, the light should move an average of 16 steps in same direction before changing. Essentially, then, the generator produced a series of 32 random time intervals and the subjects's task was to lengthen tile odd-numbered intervals and shorten the others. At end of 16 pairs, display counters gave number of Hits (clockwise) and Misses respectively. As Schmidt pointed out, 96

(Alcock ) "Thus, by chaos ing a factorable seed number we can pick out a section of the number chain which is favorable for success in the exper iment . And s ince each section used in a test run comprises only about 1/1024 of the total chain length, there is sufficient opportunity for such favorable sections to occur". (p.91) (It is interesting to note that that comment closely relates to what I have been calling attention to with regard to the problem of free-play and optional starting!) The subjects, as is so often the case with Schmidt~s experiments, were a k ind of ragtag lot . There were two groups; there were l' subjects in Group U which was predominantly Unselected (why only predominantly we are not told ~ and 4 subjects in Group S. S indicating that these were subjects who had been Selected because they appeared to be particularly promising. One of them 'was a newcomer who impressed the experimenter with his confidence and his proficiency in martial arts" (p.94~!" In the main experiment, 100 test runs were run with Group U. and another 50 runs were conducted with Group S. Subjects could participate in more than one session. Prior to running the subjects, two blocks of 100 and 50 random numbers (S and U respectively) were generated using radioactive decay, stored in a computer and printed out on the com- puter. A template was attached to the printer so that Schmidt could only see the seed numbers in the odd numbered columns; these he read aloud; he then closed his eyes and tore off paper and put in envelope for storage. (What about clairvoyance?!) In play sessions, random numbers were obtained by activating the generator in the machine; for the other sessions, the algorithm was fueled by a seed number from the memory block; no seed number was used twice. Most sessions began with play runs. After the play runs , flexible number of sessions, (on average, 8) were conducted. The decision when to end a session was "made rather subjectively, depending on the scores and the subject's and experimenter's mood and confidence. In a few cases where the subject appeared uncomfortable and prone to psi-missing under all conditions the session was terminated after the play runs, This of course is a subtle form of data selection. Subjects who seem incapable of doing well are eliminated. Secur i ty: not ment i oned . Randomization controls: None mentioned. 97

(Alcock) Results: Schmidt analyzed all runs together, for each group, and then separately analyzed only ten preinspected runs separately. He reported significant departures from chance expectation for both the S group and the U group (p<.0005, p<.05 respectively) . The PK ef feet was found with both the preinspected and the uninspected seed numbers for the S group; although the departures for all runs and for only the preinspected runs were in the same direction for the U group, only that for all runs was significant. Evaluation: The quality is in many ways improved over earlier studies, but there are still the basic problems of of randomization checks (none mentioned) and optional starting following free play. Multiple Zs increase the likelihood of Type I error above the stated levels, and given that the Zs (or CRs, as Schmidt calls them) are not very big, this is of serious concern as well. OVERALL JUDGEMENT : Once again, this paper would be unlikely to be accepted for publication in a good ps ycho l ogy, qu i te ape r ~ f r om i ts parapsycholgoical nature. Schmidt, H. tl985). Addition effect for PK on are-recorded targets. While this study receives points for imagination and creativity, it is very poor from a methodological viewpoint. Schmidt's research question in this instance is what happens when two consecutive PK efforts are made in the attempt to influence the same pre-recorded binary events. Do the two efforts contribute equally to the outcome, or does the first have the stronger effect, in line with Schmidt's "quantum collapse model". There are three experiments included in this report. In the f irst, Schmidt is both experimenter and sole sub ject . In the other two, PK efforts are made successively by two subjects, a test subject and a control subject. The control subject attempted to inf luence the binary events in some cases in the same direct ion as the test subject, and in some cases in the opposite direction. Schmidt, again the sole experimenter, is also the test subject in each case! Schmidt inf arms us that: " I had dec ided i n ad`,ance ~ o base the f i na ~ conclusions ... on the performance of the test subject only, because neither of the control subjects hack previously shown interesting scores"' (p. 238)! He found that when he went f irst, the cumulative PK score increased, while when he went second, there was no signif icant difference from chance. These results he concluded, support his quantum collapse model. Ran<3omi zat i on check s: None descr i bed . 98

~ Al cock ~ Evaluation: Given that Schmidt Is both experimenter and subject, again this shot be viewed as nothing other than a pi lot study. OVERALL JtlDGEMENT: This is a poorly executed experiment. It would have no place in a good psychology journal, quite apart from its parapsycho ~ og i ca ~ theme . Eghmidt' H. Morris, R.L. ~ & Rudolph, L. (1986) Channeling evidence for a psychok inet ic ef feet to independent observers . This study is described by its authors as "an experiment ~ n psychokinesis, performed under unusually tightly controlled conditions. In particular, the exper imenter was supervised by observers from another laboratory such that negl igence and even fraud by the exper imenter could be ruled out as an explanation of the observed e f f ects . " It involved a PK test using prerecorded random seed numbers in an attempt to channel psi evidence from Schmidt's lab in San Antonio to two independent observers (Morris and Rudolph) at Syracuse University. There were a number of subjects involved: Schmidt himself contributed substantial (unstated) number of trials. There were ten sections of test runs; Schmidt was the sole subject in four of them, and one of two sub jects in three others . Another involved a s ingle subject, another involved two subjects, and a third involved six. The methodology was as follows: ~ . Schmidt used a computer with geiger counter to generate and pr int supply of truly random six-digit seed numbers. 2. At start of each section, Schmidt decided on number of test runs t`: be made, and on which of three test arrangements to use . ~ The three arrangements were SWINGl and SWING2, two computer programmer which displayed a pendulum on the monitor whose amplitude was governed by the series of Os and is provided by the sequence generated by an aigor ithm us ing the seed number, and CLICK, a program which provided aud i tor y feedback instead of visual. SWINGl was used twice, SWING2 was used s i.Y times, and CLICK was used twice ~ . 3. Schmidt then sent a corresponding number of seed numbers tothe f irst observer, al, and also informed 02 by telephone of the number o f trials and the test arrangement . 02 had already received either t'- ~ corresponding computer (! ~ or the programme to calculate the scores for the seed numbers. 4 . 02 used his own electronic noise REG to generate a sequence ·, f binary decisions ~ H or L I, and for each pair of see] numbers, the ~ i: At; 99

(Alcock) was labelled on the basis of this number, and the other was the opposite. 5. Schmidt obtained the list of H-Ls and then gave subjects a list of seed numbers along with the target assignments, and a computer so that they could work at home at their convenience. The subjects were instructed to try to influence the outcome so, in effect, to produce a greater correlation between the H--L assignments and the order in the pairs of seed numbers. 6 Once a section was completed, the observers were informed that they could now use their computer to calculate the scores for the seed numb- ers. There were various (prespecified) numbers of trials in each section, but in each trial, a pair of seed numbers was the basic unit, and one calculated the difference between the score for the H number and the score for the L number and this gave the basic datum. Randomness checks: None were really needed, in that comparison is between H and L within each pair. Only if in some way there was a correlation between the two randomization procedures (that yielding the seed number and that yielding the H-Ls) would there be a problem, and It is difficult to imagine such a corelation. Results: If there is no departure from chance expectation, then we should expect that the mean pair-score does not differ significantly from zero. The authors used a rank-order test, and calculated a z-statistic for each of the ten sections. Eight of the ten did not differ significantly from expectation, and the other two did, but only at the .05 level, one-tailed. When all the z-scores were combined, it was found that the resultant z was significant at the .003 level. (In fact, it was not correct to combine the z-scores in the manner in which it was done because of differing degrees of freedom; Zs based on large numbers of scores were given the same weight as Zs based on smaller samples. However, I was able to obtain the raw data and when tile entire data set is analysed, with no regard for its division into ten subgroups, a significant overall deviation from what would be expected by chance is still evident; Z=2.2, p< .02). (Note: the ten sections could be taken as ten independent attempts to demonstrate the effect, only two of which were significant and then only at the .05 level). . ~ ., _ _ _ ~ i_ ~ ~ ~ ~ ~ ~ ~ ~ ~ Evaluation: Although the effect is not all that large, this study is s much better designed and executed than the earlier studies that at least one has to concede that replication attempts should be mad.-. This is not to say that psi has been demonstrated, for even the authors speak only of an "anomalous correlation", and in that spirit, fine should postpone any further interpretation or judgement urn ; replication by lndepen`5e~t experimenters can be produced. Nonetheless, although the authors show more circumspection tiers has Schmidt done in the past when acting alone, and although tile' 100

( Al cock ) indicate that really all they mean by psychokinesis in this case is an "anomalous correlation, not understandable in terms of current physics" (p. iB ), clearly they are suggesting that either the sub jects or the observer who calculated the random sequence of H and L pairs had some kind of mental influence on the outcome; otherwise, why use subjects at all? I f one begins, instead of begging the question by assuming that such mental inf luence exists, by assuming that the "effect" has already been produced once the H and L pairs are assigned, one has a better handle on the mystery. Otherwise, i f one is to cons ider that the sub ject may have had an ef feet, one runs into circularity immediate' y. Since it is agreed that the algorithm is inviolate, so that a given seed number always generates the same score, and since it is also assumed that the H or L assignment does not reverse itself as a result of the subject's actions, then what can change? Only the seed number itself, which was selected by a truly random process . The implication is that the subject, through what appears essent- lally to be "wishing", is able to inf luence a sub-atomic process which occurred at some time in the past in order that the emission of a part- icle will generate a six-digit number which will bear some desired relation to another six-digit number. However, the subject cannot know the nature of this desired relationship, for these numbers are merely seed numbers which ultimately generate other numbers, which are them- selves bile sub ject of interest; the order of a pair of seed numbers is not directly related to the order of the pair of resulting numbers, and it is this latter order which is of interest. So, the subject's task is an extremely complex one, one which the human mind by itself would be unable to master, but one, we are asked to believe, is somehow accomplished, at least on some trials, by the marvelous facility of simply wishing for it and leaving the rest to psi. Although this particular piece of research is much better in design and execution than any of the previous studies, nonetheless it is still seriously marred by methodological sloppiness and unnecessary complexity. Why, for example, use three different tasks, and run varying numbers of trials with each, and then mix all the data together? Why was the use of these tasks not decided in advance, rather than apparently being left to the whim of the experimenter, who informed the observers during the experiment as to what task was being employed at a given time? Why did the experimenter himself find it necessary to be a subject for a substantial proportion of the trials? Why were some sections run with Schmidt alone as subject, while others involved up to six different subjects? Why were ten "sections" run and then blended together? In this particular case, given that the subjects are not in a position to really do anything, except, supposedly, by psychic means, this sloppiness in methodology i s probably irrelevant, as is the fact that the exper imenter, Schmidt, himself contributed a substantial proportion of the data. However, such sloppiness does not generate great conf idence in the exper imenter . The complex i ty i s need less; the teas i c pa i r -score i s the d i f f e r e nce between two scores which are themselves the results of an aigor i tom 101

~ Alcock ~ which is started of f by a randomly chosen seed number . Yet, the aigor- ithm apparently generates a ser ice of binary O ' s and 1 ' s which are used to control the presenta~cion of either the pendulum or the clicks. Apparently 128 such b nary bits are used f or each tr ial, anti so one might expect that the "score" for a trial would be upper-boundec] by 128. However, such is not the case, as use of the BASIC algorithm or examination of the example of two scores demonstrates. It would have been so much easier simply to use one task, to have each subject perform for a f ixed number of tr ials, to use the sum of binary bits as the score, and so f orth . Obviously, it would have made sense in any normal psychological exper iment to have a control condition where no sub jects were used at all: just analyze the data at this point and compare them with what is generated when subjects are involved. However, in parapsychological research, it might be argued that even if the controls showed simi lar signif icant differences, that the differences were brought about by the psychic energies of, say, the observer who used his random generator to generate the target assignments. Indeed, in this report the authors, this is considered: "One might even wonder whether the PK effect did not enter through the second observer, subconsciously forcing his random generator Into producing favorable target assignments" (p. 183. That, of course, would involve clairvoyantly viewing the list of seed numbers and, perhaps by precognition or clairvoyance, determining what the resulting score will be once the seed is fed into the aigor ithm. One would have to do this for each pair of numbers and then, after deciding which resultant score is the higher, bring psychic influence to bear on the electronic noise in such a way that it would cause the necessary binary digit to be generated. This is not only quite ~ mean feat, but it is done repetitively during the session, although not always accurately, for the deviation from chance although significant statistically is not dramatic by any means. This process sounds well beyond the ability of the conscious mind, and it would seem unlikely that the 'unconscious" mind could do any better. However, modern parapsychological theorizing suggests that psi operates in a "goal-oriented" fashion, that one does not go through the intricate kind of calculation and analysis that I have just adumbrated. One simply desires an outcome, and that is enough. OVERAL L JUDGEME[JT: This study is much better cles igned and executed than ear 1 i er Schmidt studies. The observed effect was relatively small, and in the light of unnecessary methodological sloppiness and complexity, one would expect that the authors would want to attempt to run a more ref ined experiment, with a control group in which no subjects serve, i n 102

(Alcock) order to try to understand the cause of the correlation, if it is replicated. It is far too early' in my view,. to begin speculating about psi' even though it is not easy to come up with an explanation for the (somewhat marginal) results on the basis of the report. 103 ~ .

~ Alcock ~ APPENDIX II _~ WORK S S TUD Y RANDOM I Z. AT I ON CHECK S 1969a Five million numbers were generated by the REG for control purposes, and the frequency of all four numbers and all sixteen sequential pairs were calculated and did not differ significantly from chance expectation. These f ive million were recorded on lOO different days, '"preferably ~ insect ly af ter the exper imental sess ions " . I t may have been preferable to always do such a check immediately before the session, instead of "preferably after". [Note that even that would not be an adequate control . Hansel 's idea about general i ng two runs each t ime and randomly se lect i ng one f or the actual target and the other for a control would seem much better ~ . 19 69b 19 70a 19 7 Ob There were only 39 sess i ons, and we are not told over how many days these sessions were spread. We are given no information about the relationship between the control runs and the tests except for the "preferably after" comment. The randomness check employed is not described, but reference in this regard is made to an unpublished paper. cat: ~ hours per night for 24 nights, lamp outside, system left running. no bias in 691200 trials (Note - sessions were only i/2 hour in length; no short term checks). Between sessions, we are told, machine left running continuously to verify (in some unspecified manner) the lack of bias roaches: RNG left running each night after PK test; no bias found. both generator outputs used equal number of t Ames ~ con produce +l (shock) (Not explained wheedler the reversal we.; made half way through experiment, ox at various times ~ . 4, 000, 000 numbers generated on many different days ~ not speci f fed what was relationship of these days to exper imenta ~ sessions ~ . Number of his, -is, and number of f l id examined . Also <divided the numbers into 10, 000 sequences I, f 400 and looked at number of +l, -l and f ~ ips . The outcome `: ~ this was consistent with normal distribution. [But what about relationship between 400 sequences? Do a number ,, f high 400s occur in a row, for instance? ~ After first half of confirmatory test, the Jcwo outputs of tall generator were interchanged internally- so any bias would ~ ~ reversed (we are not told what the breakdown of scores were pre and post this change. could it be, for example, that to deviation was highly negative pre-change, and positive po=~- 104

( Alcock ) 1970c change, co give an overall negative score, but one much less impressive than in earlier studies (1969a,b)? No experimer~s reported here. This is a description of his bi nary RNG. He discusses the randomization check: N+ = number of generated +Is N- = Slumber of generated -ls F = number of flips For a random sequence, the variables X= (SORT 1/N)(N+ - N-) Y- (SORT 4/N)(F-N/2) leave independent normal distributions with Xmean = Ymean = 0 X2mean = Y2mean = (XY)mean = 0 The first randomness check involves counting, for one long generated sequence, N+ , N-, and ~ and checking to see that X2 and Y2 are not unduly large. Secondly, one might generate a certain number, S. of number sequences of length N and record the S X-values and Y-values obtained. These should have a normal distribution, which might be evaluated by a goodness-of-fit test. 1972 (with Pantas) No mention of randomization checks. 1973 RNG left unattended for long periods, usually overnight; numbers of N+, N- and flips counted. No doublets required, since there are only two states. p. 108: "Depending on whether the experimenter had set the +1 or the -l as the goal, this number were shown in the display as a "hit" and the other number as a "miss"". He said that each was used equally often. No indication of whether or I-,.: t the target was alternated from session to session or whatever; in any case this would not change the bias prober,. 1974 1976 1978 No randomization checks mentioned. Randomness tests at the completion of the sessions ware consistent with the theoretically expected average run lengths of 64. No randomness checks were mentioned. 1978 (with Terry) Control tapes were found to have non-significa. bias, yet an extensive randomness test at the completion <' f the experiments indicated no such bias. However, it was 12 times as long as the random series generated for a set ot I;; runs. 9 7 9 None ment i oned 105

~ Alcock ~ 19 ~ ~ None ment i oned 19 ~ 5 None ment i ones 9 8 6 No t requ i r ed 106

REFERENCES Alcock, J.E. 1985 Parapsychology as a "spiritual science". Pp. 537-568 in P. Kurtz, ea., A Skeptic's Handbook of Parapsychology Buf falo: Prometheus Books . Calkins, J. 1980 Comments. Zetetic Scholar 6: 77-80 . Bisaha, J.P. & Dunne, B.J. 1979 Multiple subject and long-distance precognitive remote viewing of geographical locations. Pp. 109-124 in C.T. Tart, H.E. Puthoff, & R. Targ, eds., Hlnd at large. New York: Praeger. Dunne, B. & Bisaha, J.P. 1979 Precognitive remote viewing in the Chicago area: A replication of the Stanford experiment. Journal of Parapsychology 43:17-30. Dunne, B.J., Jahn, R.G. & Nelson, R.D. 1983 Precognitive remote perception. Technical Note PEAR 83003. Engineering Anomalies Research Laboratory, School of Engineering/Applied Science, Princeton University, Princeton, N.J. (178 pp. Estes, W.K. 1976 The cognitive side of probability learning. E:ycholool- Ca 1 Bu l l e t i n 8 3 ( 1 3: 3 7 -6 4 . Hansel, H. 1980 ESP and Parapsychology: A Critical Re-Evaluatiorl. Buf falo: Prometheus Books . 107

~ Alcock 3 Hyman, R. 1977 Psychics and scientists: "Mind-reach" and remote viewing. The Humanist XXXVII(3) :6-20. 19 81 Further comments on Schmidt ' ~ PK exper iments . The Skeptical Inguirer V(3) :34-41. Jahn, R.G., Nelson, R.D. & Dunne, B.J. 1985 Variance effects in REG series score distributions. Pap- the Parapsycho log i ca ~ Assoc i at i on {Jnivers ity, Bedford, MA. E.P. & Swariff, P. Karnes, E.W., 19 79 Karnes,E.W. & 19 79 er presented at convent i on, Tuf ts Ballou, J., Susman, Remote viewing: Failures to replicate with control comparisons . Psychological Reports, 45: 963-973 . Susman, E. P . Remote viewing: A response bias interpretat ion . Psychological - Reports 4 4: 471-479 . Karnes, E.W., Susman, E.P., Klusman, P. & Turcotte, L. 1980 Failures to replicate remote-viewing using psychic sub j ects . Zetet i c Scho lar 6: 6 6 - 7 6 . Kurtz, P. 1986 The Transcendental Temptation. Buffalo: Prometheus Books . Marks, D . 19 81a Sensory cues invalidate remote viewing experiments. Nature 292:177. 198ib On the review of The Psychology of the Psychic: 108

( Al cock ) reply to Dr. Morris. Journal of the American Society for Esychical Research 75 :197-203 . Marks, D . & Karnmann, R . 1978 Information transmission in remote viewing experiments. Nature 274 680-681. 1980 The Psychology of the Psychic. Buf falo: Prometheus Book s . Marks, D. & Scott, C. 1986 Remote viewing exposed. Nature, 319:444. Morris, R.L. 1980 Some comments on the assessment of parapsychological stud ies: A review of The Psycholoc~y of the Psych ic, by David Marks and Richard Kammann. Journal of the Amer ican Society for Psychical Research 74:425-443. 1981 Dr. Morris replies to Dr. Marks. Journal of the American Society for Psychical Research, 75:203-207. Nelson, R.D., Dunne, B.J. & Jahn, R. 1984 An REG experiment with large data base capabil ity, III: Operator related anomalies. Technical Note PEAR ~ 4 0 0 3, Pr i nce ton Eng ~ neer i ng Anoma ~ i es Research, Scho `~ ~ of Engineering/Appliec] Science, Princeton Univer- sity. (159 pp. Palmer, J. 1985 An evaluative report on the current status of pare psychology. Paper prepared for the United States Army 109

1981 Radtke, R.C., 1971 Schlitz, M. & 1980 1981 (Alcock) Research Institute for the Behavioral and Social Sciences. (Fine' Draft). Puthoff, H.E. & Targ, R. 1979 A perceptual channel for information transfer over kilometer distances: Historical perspective and recent research. Pp. 13-76 in C.T. Tart, H.E. Puthoff, & R. Targ, eds, Hind at large. New York: Praeger. Rebuttal of criticisms of remote viewing experi- ments. Nature 292:388. Jacobs, L . L . & Goede I, G . D . Frequency ~ iscr imination as a function of frequency of repetition and tr ials . Journal of E:xper imental Psychol - ogy 89:76-84. Gruber, E. Transcont inental remote viewing . Journal of Para - psychology 4 4: 305-317 . Transcontinental remote viewing: A re judging. your na 1 0 f Parapsycho 1 ogy 4 5: 2 3 3 - 2 3 7 . Schlitz, M. & Haight, J.M. 1984 Remote viewing revisited: An intrasubject reE~ c~ ~ ~ i on . Jour na ~ o f Parapsycho ~ ogy 4 8: 3 9 - 4 9 . Schmidt, H. 1969a Precognition of a quantum process. Journal of Par~- psycholocy 33:99-108. 1969b Clairvoyance tests with a machine. Journal of P.~l_~_ psychology 33:300-306. ~0

19 70a 1970b 1970 1973 1974 1975 1976 1978 19 79a 19 79b ~ Alcock ~ A PK test with electronic equipment. Journal of Para- psychology, 34: 175-~81. A quantum mechanical random number generator for ps tests . Journal of Parapsychology, 34: 219-224 . PK exper iments with animals as sub jects . Journal of Parapsychology, 34: 255-261. PK tests with a high-speed random number generator. Jou- rnal of Parapsychology, 37 :105-~8. Compar ison of PK action on two di f ferent random number generators. Journal of parapsychology' 38: 47-55. Toward a mathemat ical theory of ps i . Journal of the Amer ican Society for Psychical Research 69:301 -319 . PK ef feet on pre-recorclec] targets . Journal of the Amer lean Society for Psychical Research 70: 267-291. A take-home test in PK with pre-recorded targets. Pp. 31-36 in W.G.Roll, ea., Research in Parapsychology 1977. Metuchen, N. J .: The Scarecrow Press . Search for psi fluctuations in a PK test with cocks roaches. Pp. 72-79 in W.G. Roll, ea., Research in Parapsychology 1978. Metuchen, N.J.: The Scarecrow Press . Use of stroboscopic ~ ight as rewarding feedback in a PK test with pre-recorded and momentar fly-generate`] random events. Pp. ~15-~17 in W.G. Roll, ea., Research

~'4 ( Alcock ) ire Parapsychology 1978 . Metuchen, N. J Press . Evidence for direct interaction between the human mind and external quantum processes. Pp. 207-220 in C. T. Tart, H.E. Puthof f, & R. Targ ads ., Mind atiarge . New York: Praeger. PK tests with pre-recorded and pre-inspected seed numbe rs . Jour na l o f Parapsycho l ogy, 4 5: 8 7 -9 8 . Addition of feet for PK on prerecorded targets . Journal of Parapsychology 49: 29-244. Schmidt, H . & Pantas, L . 1972 Psi tests with internally different machines. Journal of Parapsychology 36: 222-232. Schmidt, H. Morris, R.L., & Ru<3olph, L. 1986 Channeling evidence for a PK effect to independent observers. Journal of Parapsychology 50 :1-16. Stanford, R. G. 1977 Experimental psychokinesis: a review from diverse perspectives. Pp. 324-381 in B.B.Wolman' ed. ~ Handbook of Parapsychology. New York: Van Nostrand. Targ, R . & Puthof f, H.E. 1974 Information transfer under conditions of sensory shielding. Nature 251: 602-607 . Mi nd-reach . New York: De lacorte . 19 79c 19 81 19 85 ,: The Scarecrow 1977 112

(Alcock3 Targ, R., Puthoff, 1979 Direct Tart, C.T. H.E., & May, E.C. perception of remote geographical locations. Pp. 13-76 in C.T. Tart, H.E. Puthoff, ~ R. Targ, ads., Mind at larch. New York: Praeger. 1980 Comments on Karnes et al., 1980. 6:85-86. Tart, C. T., Puthof f, H . E. & Targ, R . 19 ~ O I nf ormat i on Nature 284:191. Terry, J. & Schmidt, H. 1978 Conscious targets. Pp. 36-41 Zetetic Scholar transmiss i on in remote viewing exper iments . and unconscious PK tests with prerecorded in W.G. Roll DaraDsMcholocy 1977 Fletuchen, NJ: _ —- _ _ ~ ~ _ 113 ea.' Research in Scarecrow.

1981 Radtke, R.C., 1971 Schlitz, M. & 1980 1981 Schlitz, M. & 1984 (Alcock) Research Institute for the Behavioral and Social Sciences. (Fine' Draft ~ . Puthof f, H. E. & Targ, R . 1979 A perceptual channel for information transfer over kilometer distances: Historical perspective and recent research, Pp. 13-76 in C.T. Tart, H.E. Puthoff, & R. Targ' eds' Hind at large. New York : Praeger. Rebuttal of criticisms of remote viewing exper i ments. Nature 292:388. Jacoby, L.L. & Goedel, G.D. Frequency discrimination as a function of frequency of repetition and trials. Journal of Experimental Psychol ogy 89:78-84. Gruber, E. Transcont inental remote viewing . Journal of Para - osychology 44:305-317. Transcontinental remote viewing: A re judging. Four na 1 o f Parapsycho 1 ogy 4 5: 2 3 3 - 2 3 7 . Haight, J.M. Remote viewing revisited: An intrasubject rep~- ~ion. Journal 0 f Parapsychology 4B: 39-49 . Schmidt, H. 1969a Precognition of a quantum process. Journal of Para psycholocy 33:99-108. l969b Clairvoyance tests with a machine. Journal of P.__ psychology 33:300-306. 110

(Alcock) Hyman, R. 1977 Psychics and scientists: "Mind-reach" and remote viewing. The Humanist XXXVII(3):6-20. 1981 Further comments on Schmidt's PK experiments The Skeptical Ingulrer V(3):34-41. Jahn, R.G., Nelson, R.D. & Dunne, B.J. 1985 Variance effects in REG series score distributions. Pap- er presented at the Parapsychological Association convention, Tufts University, Medford, MA. Karnes, E.W., Ballou, J., Susman, E.P. & Swarlff, P. 1979 Remote viewing: Failures to replicate with control comparisons. Psychological Reports, 45:963-973. Karnes,E.W. & Susman, E.P. 1979 Remote viewing: A response bias interpretation. Psychological - Reports 44:471-479 . Karnes, E.W., Susman, E.P., Klusman, P. & Turcotte, L. 1980 Failures to replicate remote-viewing using psychic subjects. Zetetic Scholar 6:66-76. Kurtz, P. 1986 The Transcendental Temptation. Buffalo: Prometheus Books. Marks, D. 1981a Sensory cues invalidate remote viewing experiments. Nature 292:177. 1981b on the review of The Psychology of the Psychic: A 108

( Al cock ) reply to Dr. Morris. Journal of the American Society for Esychical Research 75 :197-203 . Marks, D . & Karnmann, R . 1978 Information transmission in remote viewing experiments. Nature 274 680-681. 1980 The Psychology of the Psychic. Buf falo: Prometheus Book s . Marks, D. & Scott, C. 1986 Remote viewing exposed. Nature, 319:444. Morris, R.L. 1980 Some comments on the assessment of parapsychological stud ies: A review of The Psycholoc~y of the Psych ic, by David Marks and Richard Kammann. Journal of the Amer ican Society for Psychical Research 74:425-443. 1981 Dr. Morris replies to Dr. Marks. Journal of the American Society for Psychical Research, 75:203-207. Nelson, R.D., Dunne, B.J. & Jahn, R. 1984 An REG experiment with large data base capabil ity, III: Operator related anomalies. Technical Note PEAR ~ 4 0 0 3, Pr i nce ton Eng ~ neer i ng Anoma ~ i es Research, Scho `~ ~ of Engineering/Appliec] Science, Princeton Univer- sity. (159 pp. Palmer, J. 1985 An evaluative report on the current status of pare psychology. Paper prepared for the United States Army 109

1981 Radtke, R.C., 1971 Schlitz, M. & 1980 1981 Schlitz, M. & 1984 (Alcock) Research Institute for the Behavioral and Social Sciences. (Fine' Draft ~ . Puthof f, H. E. & Targ, R . 1979 A perceptual channel for information transfer over kilometer distances: Historical perspective and recent research, Pp. 13-76 in C.T. Tart, H.E. Puthoff, & R. Targ' eds' Hind at large. New York : Praeger. Rebuttal of criticisms of remote viewing exper i- ments. Nature 292:388. Jacoby, L.L. & Goedel, G.D. Frequency discrimination as a function of frequency of repetition and trials. Journal of Experimental Psychol- ogy 89:78-84. Gruber, E. Transcont inental remote viewing . Journal of Para - osychology 44:305-317. Transcontinental remote viewing: A re judging. Four na 1 o f Parapsycho 1 ogy 4 5: 2 3 3 - 2 3 7 . Haight, J.M. Remote viewing revisited: An intrasubject rep~- ~ion. Journal 0 f Parapsychology 4B: 39-49 . Schmidt, H. 1969a Precognition of a quantum process. Journal of Para- psycholocy 33:99-108. l969b Clairvoyance tests with a machine. Journal of P.__ psychology 33:300-306. 110

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